U.S. Department of Justice 


Bureau of Justice Statistics 


Indicators of crime 


and criminal justice: 


Quantitative studies 


NCJ-62349, June 1980 

Edited by 

STEPHEN E. FIENBERG 

Department of Statistics 

and Department of Social Science 

Carnegie- Mellon University 

ALBERT J. REISS, JR. 

Department of Sociology 

Yale University 

PROPERTY OF 

National Crimina! Justice Aelerence Service (PdCJRS) 

Box 6003 

Wockville, hPiD 20849-66'00 

For sale by the Superintendent of Doculuents, U.S. Government Prilltiug OWce, Wasliington, D.C. 20402 
U.S; Department of Justice 

Bureau of Justice Statistics 

Harry A. Sum, Ph. D. 

Director 

The Social Science Research Council is a 

private nonprofit organization formed for 

the purpose of advancing research in the 

social sciences. It emphasizes the planning, 

appraisal, and stimulation of research that 

offers promise of increasing knowledge in 

social science or of increasing its usefulness 

to society. It is also concerned with the 

develoument of better research methods. 

irnpro;ement of the quality and accessibility of materials for research by social scientists, and augmentation of resources and 

facilities for their research. 

The Council's Center for Coordination of 

Research on Social Indicators was established in September 1972, under a grant 

from the Division of Social Sciences, National Science Foundation (grant number 

GS-34219; currently SOC-77-21686). The 

Center's purpose is to ahance the contribution of social science research to the development of a broad range of indicators of 

social change, in response to current and 

anticipated demands from both research 

and policy communities. 

Library of Congress Cataloging in Publication Data 

Main entry under title: 

Indicators of crime and criminal justice. 

Based on research initiated during the Workshop in 

Criminal Justice Statistics, held in the summer of 1975 

by the Social Science Research Council. 

"NCJ-62349." 

Includes bibliographical references. 

Supt of Docs. no.: J 29.2:1n2 

1. Criminal statistics-Addresses, essays, lectures. 

I. Fienberg, Stephen E. 11. Reiss, Albert 

J. 111. Workshop in Criminal Justice Statistics, 

1975. 1V. Social Science Research Council. 

HV6018.152 364 80-607926 

This project was supported by Grant No. 75-SS-99- 

6017, awarded to the Social Science Research Council 

by the Statistics Division, National Criminal Justice 

Information and Statistics Service, Law Enforcement 

Assistance Administration(n0w Bureau of Justice Statistics), U.S. Department of Justice, under the Omnibus 

Crime Control and Safe Streets Act of 1968, as 

amended. The project,entitlednWorkshopandFellowship in Criminal Justice Statistics," was directed forthe 

Social Science Research Council by David Seidman 

and monitored by Paul D. White of BJS. Points of view 

or opinions stated in this document are those of the 

author(s) and do not necessarily represent the official 

position or policies of the U.S. Department ofJustice. 

LEAA authorizes any person to reproduce, publish, 

translate, or otherwise useallor any part of the material 

in this publication, with the exception of those items 

indicating that they are copyrighted by or reprinted by 

permission from any other source. 
Preface 

The Social Science Research Council's 

Center for Coordination of Research on 

Social Indicators, organized in 1972, has 

had an ongoing interest in promotingquality research in the area of criminal justice 

statistics, especially at a national level. To 

this end, the Center's Advisory and Planning Committee created in 1973 a special 

Subcommittee on Criminal Justice Statistics, whose focus has been on understanding and measuring aspects of crime 

and the criminal justice system. 

The present volume can be traced back to a 

meeting of the members of the Subcommittee with staff at the Law Enforcement 

Assistance Administration (LEAA) to discuss research projects of mutual interest. 

The two of us (Stephen E. Fienberg and 

Albert J. Reiss, Jr.) were convinced that an 

upgrading of the quality of research in the 

criminal justice area could be affected 

through the recruitment of statisticians and 

other quantitative social scientists to work 

on interesting statistical modelling and 

analysis projects in the area. We therefore 

proposed to hold a workshop focussing on 

the methodological and theoretical problems involved in the measurement af crime 

and its effects on society. 

Thus it was that in the summer of 1975, the 

Social Science Research Council, with 

funding from LEAA* (now the Bureau of 

Justice Statistics), organized a month-long 

Workshop in Criminal Justice Statistics. 

The workshop brought together three 

groups: a faculty composed of seven 

experts in criminal justice; seven participants who were young academic statisticians, sociologists, and psychologists; 

and six government professionals. 

The workshop's program of activities 

started with a series of lectures and seminars and concluded with the organization 

of the faculty and the participants into six 

working groups. Among the topics covered 

at the plenary meetings were conceptions 

of the criminal justice system, data sources, 

research approaches, methodological and 

substantive problems, and theoretical 

issues. The intensive interchange at these 

sessions sparked a high degree of interest in 

the six working groups, each of which then 

undertook a concentrated exploration of a 

problem area in criminal justice research. 

'Grant No. 7533-994017. 

The topics on which they focused were the 

treatment of data in victimization surveys; 

measurement and experimental design in 

the study of police effectiveness; the sentencing process; decisionmaking by the 

U.S. Board of Parole; the deterrent effect 

of capital punishment; and the problem of 

designing a model of the criminal justice 

system. 

The papers in the present volume are a 

direct outgrowth of research initiated 

during or as a result of the workshop activities. Earlier drafts of many of the papers 

were presented and discussed at a workshop reunion which took the form of a conference held in the fall of 1977, again 

sponsored by LEAA. The first paper in this 

volume reports on the highlights of that 

conference, and provides an overview to 

the frontiers of quantitative research in this 

area. The remaining sections of the volume 

are organized in large part around the 

research produced by the six working 

groups from 'the workshop. 

The faculty of the workshop consisted of 

Albert D. Biderman, Bureau of Social 

Science Research (Washington, D.C.); 

Alfred ~lumxn,Carnegie-Mellon University; John Clark, University of Minnesota; 

~ichaelJ. Hindelang, State University of 

New York at Albany; Albert J. Reiss, Jr., 

Yale University; Richard Sparks, Rutgers 

University; and Leslie T. Wilkins, State 

University of New York at Albany. 

The social scientist participants in the 

workshop were David W. Britt, Florida 

Atlantic University (currently at Nova University); William B. Fairley, Harvard University (currently a private consultant); 

Stephen E. Fienberg, University of Minnesota; Gary G. Koch, University of North 

Carolina; Kinley Larntz, University of 

Minnesota; Colin Loftin, Brown University (currently at the University of Michigan); and Howard Wainer, University of 

Chicago (currently at the Bureau of Social 

Science Research). 

Government professionals participating in 

the workshop were Ken Brimmer, Mimi 

Cantwell, Linda Murphy, Tom Petersik, 

and J. Frederick Shenk, all of the U.S. 

Bureau of the Census; and Cynthia 

Turnure, Minnesota Governor's Commission on Crime Prevention and Control. 

One of the most pleasing outcomes of'the 

workshop (at least to us) has been the continuing work of the participants and faculty 

on methodological problems in criminal 

justice research. They have been intimately 

involved in such activities as: (a) the 

National Academy of Sciencies-National 

Research Council's Committee on Law 

Enforcement and Criminal Justiceand that 

Committee's Panels on Deterrence and 

Incapacitation, and on Rehabilitation, (b) 

the NAS-NRC Committee on National 

Statistics and that Committee's Panel on 

the National Crime Survey, (c) the American Statistical Association's Committee on 

Law and Criminal Justice Statistics, and 

(d) SSRC's Advisory and Planning Committee on Social Indicators. They have also 

initiated new research projects on a wide 

variety of problems in the area. This continued activity is perhaps the best indicator 

of the success of the Workshop. 

Almost as pleasing are the many professional collaborations and personal friendships that developed among those who 

took part in the Workshop. These go far 

beyond the work reported on in this 

volume. 

We acknowledge with thanks the contributions of David Seidman of the Social 

Science Research Council, and of Elaine 

Javonovich, his assistant, who staffed the 

Workshop; and of the staff and director of 

the Council's Center for Social Indicators 

for their support and interest. Special 

thanks are due to Nancy McManus of the 

Social Science Research Council, who 

worked closely with us in structuring the 

volume, extracting manuscripts from 

authors, and copyediting the entire volume. 

Ms. McManus was responsible for seeing 

the manuscript through to completion, and 

we are indebted to her for her assistance. 

STEPHENE. RENBERG 

ALBERT J. REISS,JR. 
Abstract 

The quantitative study of criminal justice is 

a rapidly expanding field, involving the 

application of relatively sophisticated statistical methods and probabilistic models. 

This volume brings together some of the 

products of a workshop in criminal justice 

statistics sponsored by the Social Science 

Research Council and the Law Enforcement Assistance Administration (now the 

Bureau of Justice Statistics) during the 

summer of 1975. An introductory essay 

describes the highlights of a followup conference held in October 1977, at which 

workshop participants described some of 

their subsequent research. This essay provides an overview of the volume and of the 

frontiers of quantitative research in this 

area. The remaining papers consist of detailed versions of conference presentations, 

as well as reports on other related research 

in such diverse areas as: macro models for 

criminal justice planning; the deterrent 

effects of punishment on crime; effects of 

plea-bargaining on case disposition; criminal victimization and models for its 

analysis; victim proneness; parole decisionmaking, and police patrol experiments. 
Contents 

David Seidman 

Albert J. Reiss, Jr. 

Richard F. Sparks 

Albert D. Biderman 

Stephen E. Fienberg 

Albert J. Reiss. Jr. 

Stephen E. Fienberg 

Richard Perline 

Howard Wainer 

Kinley Lurntz 

David W. Britt 

Kinley Larntz 

Colin- Loftin 

Stephen S. Brier 

Stephen E. Fienberg 

Awed Blumstein 

Gary G. Koch 

Stephen E. Fienberg 

Kinley Larntz 

Albert J. Reiss, Jr. 

Preface, iii 


Abstract, iv 


Current research in criminal justice statistics: 


Report of a conference, 1 


Crime rates and victimization 

Understanding changes in crime rates, I1 


Criminal opportunities and crime rates, 18 


Notes on measurement by crime victimization surveys, 29 


Victimization and the National Crime survey 


Problems of design and analysis, 33 


Victim proneness in repeat victimization by type 


of crime, 4 1 


Statistical modelling in the analysis of repeat 


victimization, 54 


Sentencing and parole decisionmaking 

Quantitative approaches to the study of parole, 59 


Linear logistic models for the parole decisionmaking 


problem, 63 


The effects of plea bargaining on the disposition of personal 


and property crimes: A research note, 70 


The deterrent effects of punishment 

Alternative estimates of the impact of certainty and severity 


of punishment on levels of homicide in American states, 75 


Recent econometric modelling of crime and punishment: 


Support for the deterrence hypothesis?, 82 


Criminal justice planning 

A prolegomenon for a macro model for criminal justice 


planning: JUSSIM 111, 99 


Redesigning the Kansas City Preventive Patrol 


Experiment, 109 

Current research in criminal justice statistics: 


Report of a conference* 

DAVIDSEIDMAN** 

Social Science Research Council 

Washington, D. C. 

The quantitative study of crime and criminal justice is a rapidly developing field of 

research. While perhaps most of this development can be attributed at least indirectly 

to the apparent rise in crime beginning in 

the 196OYs, advances in particular areas can 

be traced to more proximate causes. The 

creation of major new data bases is perhaps 

the most obvious stimulus to quantitative 

research, and here the invention and institutionalization of victimization surveys 

have been particularly notable. There has 

been, within the criminal justice system 

itself, increased self-awareness, and this 

has stimulated attempts to rationalize the 

decisionmaking process .within the system. 

The basis of rationalization, in a number of 

instances, has been quantitative study of 

the. actual operations of the system, 

combined with attempts to develop prediction methods which would allow for new 

approaches to decision making. Finally, 

there has been increasing questioning of 

the effects of the criminal justice system on 

offenders, on the crime rate, and on society 

as a whole; this questioning has led to 

attempts to analyze quantitatively what 

those effects are, in ways which may 

provide guidance for criminal justice policy 

in the future. 

These three areas of research were intensely 

studied at the Social Science Research 

Council's Workshop in Criminal Justice 

Statistics during the summer of 1975. Subsequent to the workshop, participants 

carried out research in these areas and 

others. The conference held in October 

1977 provided an opportunity for presentation of research results and for discussion 

of research plans. The presentations and 

*A report to the Bureau of Justice Statistics by the 

Social Science Research Council, 605 Third Avenue, 

New Y ork, NY 10016, pursuant to Order Numbers0073-J-LEAA. This report is based upon working 

papers presented at the conference. The quotations 

and materials discussed will therefore not necessarily coincide with the versions of the papers 

published in this volume. 

**In September 1978 David Seidman left the Social 

Science Research Council forthe Rand Corporation, 

Washington. D.C. 

discussions do not represent the full range 

of research in criminal justice carried out 

by workshop participants since the summer of 1975, but focus on the three areas of 

research discussed above and emphasize 

research supported by the Law Enforcement Assistance Administration grant to 

the Social Science Research Council which 

made the workshop possible. 

This report draws upon both the written 

conference papers and the discussions to 

present highlights of the conference in the 

the three mainareas considered. It does not 

pretend to capture the full richness of the 

presentations, and the reader should turn 

to the conference papers for the complete 

picture. Together, the report and the 

papers provide an overview of current 

research on the frontiers of the quantitative 

study of crime and criminal justice and an 

assessment of current problems and 

directions for future research. 

Victimization studies 

MOSTPUBLISHED reports of victimization 

surveys amount to little more than calculations of "victimization rates" for populations and subpopulations for particular 

time periods. While these calculations may 

be useful, they leave unresolved certain 

conceptual issues, contribute little to an 

understanding of crime and victimization, 

and fail to exploit the full potential of the 

surveys (in particular, the longitudinal 

features of the National Crime Panel 

Survey are underexploited). Several workshop participants have been studying victimization surveys in ways which probe 

more deeply into the structures and processes underlying the data. The primary 

focus has been on problems related to multiple and series victimization and the interactions of survey design features and 

resulting data. Considerable time at the 

conference was devoted to presentation 

and discussion of this work. 

A useful introduction to problems of multiple victimization is a well-known finding 

concerning the distribution of individuals 

by number of reported victimizations 

within the reference period. Richard 

Sparks presented one version of this distribution, based on his London victimization 

survey. (See Sparks, Table 1.)' What is at 

issue here is the sense in which the overall 

victimization rate characterizes the risk of 

victimization for individuals in the group. 

If it is assumed that the overall rate represents the risk faced by individuals, then the 

distribution of individuals by number of 

victimizations ought to fit a Poisson distribution. The last column of Sparks's table 

shows the expected number of individuals 

by number of victimizations for a Poisson 

process. The standard finding emerges: 

"the numbers reporting no victimization at 

all, and the numbers reporting several incidents, are both greater than would be predicted by a Poisson distribution" (Sparks). 

This result is a starting point for speculation and investigation. Sparks, for example, points out that slightly more complicated models fit the data better. In particular, models based on either "contagion" or 

heterogeneity of victim proneness in the 

population work reasonably well. Unfortunately, the two models cannot be differentiated in cross-sectional data, which 

points to the importance of exploiting the 

longitudinal features of NCS. Sparks finds 

the contagion notion an implausible 

explanation of the data, and this discussion 

will pursue the victim proneness direction. 

If the explanation of the lack of fit of the' 

Poisson model is that individuals differ in 

their victim proneness, a logical next step is 

to sort out individuals by their degrees of 

victim proneness, and see if the Poisson 

model fits within subgroups of the population. Sparks tried this with his London 

'Cltat~onsw~thout dates refer to papers and other materials which served as the basis for conference presentations. Other citations are to materials included in the 

l~st of references at the end of th~s report. 
data. but could not find any combination 

of attributes, such as age, sex, race, or 

social class, which could be used to categorize individuals to produce subgroups 

within which the Poisson model adequately fit the data. As he notes, it is not 

surprising that these simple demographic 

variables would be insufficient. 

It is possible that the observed pattern 

actually results from measurement problems in the surveys. One such measurement 

problem has to do with series incidents. 

Typically the number of incidents in a 

series is estimated by the victims, and there 

appears to be a tendency to overestimate 

the number-a phenomenon common to a 

number of different areas of investigation. 

For a variety of reasons, incorporation of 

series victimizations into the distributions 

here considered is difficult, and their exclusion may substantially affect the shape of 

the distribution. Some indication of the 

effect can be obtained by examining such 

questions as whether series victims also 

report other victimizations, but this examination is difficult in a small cross-sectional 

survey. Another measurement problem is 

nonreporting. It may be, for example, that 

most nonreporting is by people who have 

been victims only once. Since the departures from the Poisson distribution are 

largely in the zero and one victimization 

groups, this would account for much of the 

lack of fit. Accounting for that pattern of 

nonreporting, however, is difficult. 

If the deviation from the Poisson distribution appears to be mainly a matter of too 

many people reporting no victimizations, it 

seems reasonable to fit a Poisson distribution to the distribution of those reporting 

at least one victimization, and then project 

backwards to estimate the number "belonging" in the zero victimization group 

under Poisson assumptions. The 'excess" 

actually found in that category might then 

be thought of as drawn from a population 

somehow lacking vulnerability to crime. 

The source of this immunity to crime-or 

at least to certain kinds of crime-is not 

immediately obvious. Presumably it has 

something to do with residential location 

or life style. Of course, while a model postulating an immune group and a group 

subject to Poisson process may fit thedata, 

isolating the immune group for analysis 

may not be possible, since there is no obvious way to separate it from the group 

which, as a result of the random process, 

was not victimized in the reference period. 

The plausibility of an absolutely immune 

group declines when a time perspective 

longer than the reference period of a single 

cross-sectional survey is adopted. This 

begins to suggest the importance of exploiting the over-time features of the National Crime Panel Survey. There are, of 

course, other reasons for relying upon longitudinal files of the NCS for analysis of 

multiple and series victimimtion. For one 

thing, the large number of incidents available in such files allows disaggregation to 

crime-specific victimization. For another, 

repeated interviews can be used to build 

long sequences of victimization experience, 

which allow, among other things, investigation of the stability of patterns. Finally, 

longitudinal files allow investigation of the 

time between victimizations, which may be 

important to an understanding of multiple 

victimization. 

Albert J. Reiss, Jr., has constructed what 

we believe to be the only extant working 

longitudinal file of NCS data. He presented 

some results of analysis of this file to the 

conference. These results concerned the 

relatively limited question of whether in 

repeated victimization of a given unit there 

is a propensity for repeated victimization 

by the same type of crime, or whether repeated victimization is random as to crime 

type. While the question is limited, it appears central to an understanding of victim 

proneness and multiple victimization. 

The analytical tool Reiss used is a crime 

switch matrix consisting of pairs of victjmizations, where a preceding victimization by 

type of crime is compared with a following 

victimization by type of crime. 

The construction of such a matrix presents 

a number of questions and problems. First, 

what is the unit at risk? Confining his analysis to households as units, Reiss notes that 

victimization of individuals within households may symbolically represent victimization of the household. (Similarly, 

individuals may not sharply distinguish 

household victimization from personal victimization when the focus is on personal 

victimizations. Because of the choice of 

focusing on households, Reiss's analysis is 

unaffected by this problem.) It follows that 

if the household is the unit of analysis, a researcher may either limit the analysis to 

household victimizations or include as well 

victimizations of individuals within the 

household. Reiss examined the data both 

ways. 

Second, the matrix depends upon the time 

sequence of victimizations. NCS incident 

reports record the month of nonseries victimizations. Victimizations of a household 

within a month, however, lack the information required to establish the time sequence. 

The timing of series victimizations presents 

a more complicated problem, as the NCS 

records only the month of occurrence of 

the first incident in the series (and if the 

series began before the reference period, 

the date recorded is the first month of the 

reference period). Reiss therefore had to 

impose an arbitrary time order so as to 

establish a sequence for all reported victimizations. He did this by randomly assigning 

dates within months to events, with series 

treated as single events. The error introduced into the ordering by this random 

procedure is likely to be relatively small for 

nonseries incidents, as incidents occurring 

in different months are unaffected. The 

errors introduced by treating series victimizations as single incidents and then placing 

them (at a randomly selected date) in the 

month the series begins (or the first month 

of the reference period) are harder to assess 

because of the general paucity of information about series victimizations. However, 

Reiss has found that those who report 

series victimizations are highly unlikely to 

report other victimizations, so that the 

primary effect of his treatment of series victimizations is likely to be a reduction in the 

proportion of cases in a crime switch' 

matrix which fall on the diagonal of the 

matrix (since events within a series are in 

theory all of the same kind). The significance of this will become clear as the results 

are discussed. 

A preliminary examination of the data 

(Reiss's "Victim Proneness") enables one 

to compare the distributions of victimi.zation incidents by type of crime where both 

incidents occurring in sequences and single 

victimizations are included with equivalent 

distributions not including singli victimizations. It is apparent that the distributions 

are substantially similar, which leads Reiss 

to conclude that "multiple or repeat household victims are on the whole no more 

prone to victimization by certain types of 

crime than are all victims." If multiple 

victimization reflects victim proneness, it 

nevertheless seems not to reflect proneness 

to particular types of crime. 
Reiss's crime switch matrix further exposes 

the structure of multiple victimization. As 

is perhaps clearer from a chi-squared 

analysis of the matrix, the major element of 

structure in the matrix is the heaping of 

incidents along the diagonal. The implication is that "the chances that a household 

or one or more of its members will be 

successively victimized by the same type of 

crime are greater than one would expect 

given the chances all households and their 

members have of being victimized by that 

type of crime." The analysis continues by 

examining whether the frequency of 

particular pairs depends upon which 

element of the pair occurs first. For 

example, is the sequence assault-personal 

larceny more or less frequent than the 

sequence personal larceny-assault? Reiss's 

Table 4 strongly suggests that the order 

within pairs makes no difference; that the 

structure is symmetrical with respect to 

order of occurrence. 

Reiss's paper merely establishes these elements of structure. Conference participants offered some speculative explanations. Some possible explanations turn on 

methodological artifacts: reporting definitions, response bias, interviewing techniques, and the like. More substantive 

explanations focused on the characteristics 

of locations, patterns of communication, 

and the elusive concept of victim proneness. 

It was noted that, because the NCS is a survey of household locations, there is in 

theory the opportunity to explore victim 

proneness and location proneness by 

examining over time (1) victimization experiences at locations where there is a 

change in individuals, and (2) victimization 

experiences of individuals who move out of 

a survey location. The importance of this 

kind of examination is suggested by the relationship between being victimized and 

moving. Reiss pointed out that both series 

victims and other multiple victims are 

highly likely to move. The questions which 

need to be answered are whether the high 

rate of victimization continues with a new 

household at the surveyed location and 

whether the high rate of victimization continues for the mover at a new location. 

While in theory the survey design might 

permit the first question to be addressed, in 

practice it does not, because the records do 

not carefully distinguish between new and 

old tesidents in continuing locations and 

because, in the case of new residents, no 

information is sought about victimization 

experience at the prior location. (That is, 

information is obtained which, depending 

upon the time of the move, may relate to 

the new resident's prior residence, but there 

is, in the recorded data, no way to distiilguish between victimization at the old location and victimization at the new one.) The 

second question cannot be addressed at all, 

because no attempt is made to follow 

movers to their new residential locations. It 

might be possible to approach the problem 

relatively cheaply by adding to interviews 

with new residents a set of questions designed to elicit retrospective information 

about victimization experiences, though 

recall decay problems would be a substantial obstacle to obtaining reliable information. 

Also important to questions of victim and 

location proneness is the character of the 

neighborhood of the interview location. 

Reiss has merged certain neighborhood 

characteristics onto his victimization tape, 

but what is perhaps the most important 

neighborhood characteristic for these purposes, the neighborhood crime rate, is 

unavailable. 

Some questions about these patterns of 

multiple victimization relate to the length 

of time in panel for respondents. The Reiss 

data set contains a high proportion of respondents interviewed only a small number 

of times. It seems likely thatthe proporiion 

of single victimizations would decline as, 

the sample "ages." It is also possible that 

some of the concentration on the diagonal 

of the crime switch matrix would decline, 

the pattern of victimization followed by 

victimization of the same kind declining as 

time between victimizations increases. 

Reiss in other work is examining time between victimizations, but results of that 

work were not presented at the conference. 

Stephen Fienberg has been developing 

models for analysis of victimizationdata in 

their full longitudinal structure, with particular attention to problems of multiple 

victimization and various time-related 

effects in the data, such as the effects of 

month of collection, time lag to reference 

month, and time in panel. A preliminary 

sketch of this approach is contained in section 5 of his "Victimization and the National Crime Survey: Problems of Design 

and Analysis." He expanded upon these 

ideas in a presentation at ehe conference. 

In Fienberg's view, analysis of questions of 

multiple victimization depends upon models for the occurrence of victimizations 

over time. Without necessarily suggesting 

that it represents the true underlying structure, Fienberg proposes modelling victimization as a particular form of stochastic 

point process, a semi-Markov process. 

(The Poisson process, discussed above, is a 

special case of the semi-Markov process.) 

Such a process has two main features. 

First, the probability that one is next victimized by a crime of type j depends only 

upon the crime type of which one was last a 

victim. That is, the transition from victimization state to victimization state is governed by a matrix of probabilities resembling Reiss's crime switch matrix. Second, 

the interval between victimizations is random, though the distribution of time 

between victimizations depends upon the 

current victimization state. A convenient 

feature of semi-Markov processes is that, 

for many purposes, the transition matrix 

and the time interval distributions can be 

studied separately. The model is based on 

continuous time, while victimization data 

collection is one month at a time. Integrating these two different approaches presents 

modelling, problems. 

Fienberg also notes that the hierarchical 

structure of the victimization surveys (individuals within families, families within 

households, households within locations, 

locations within neighborhoods) complicates the modelling approach. These adqed 

complications will not be discussed here. 

A fundamental question is whether the 

process is time homogeneous, or whether 

there are shifts in the process related to, 

say, time in panel or other causes. To answer this question and others relating to 

time between events, Fienberg proposes a 

research approach along the following 

lines. In order to obtain the required long 

records, he begins with a subfile of respondents with full 3%year records. Assume we 

start by considering the household as the 

unit of interest. Then there are 42 months 

in which an incident of victimization may 

be reported. As a first step, consider only 

whether the household has or has not been 

victimized within a given month, ignoring 

differences among types of crime and multiple victimization within a month. (Note 
that the NCS treatment of series victimization causes difficulties here.) Then there are 

242 possible time sequence patterns, a 

number far too large for analysis. In practice, the number of patterns found would 

probably be much smaller; Fienbergguesses 

that about 20 patterns would account for 

95 percent of the records. It would then be 

possible to examine the time patterns for 

shifts associated with time in panel. As a 

next step, households could be scored each 

month according to whether there has been 

household victimization, personal victimization, or no victimization, and the same 

kind of analysis could be done. The analysis would then continue, examining finer 

grain structure at each step. The information on time sequencing of victimizations 

generated in this way feeds back into the 

models of generation of multiple victimization which are at the heart of the investigation. The discovery of time heterogeneity in 

long records would likely allow for various 

transformations inducing homogeneity. In 

addition to casting light on the underlying 

processes, such transformations would 

provide important information about the 

interpretation of aggregate victimization 

rates in cross-sectional analysis. The problem of the ill-fitting Poisson can be addressed, and records sorted in ways allowing examination of victim proneness. 

Several of the conferees questioned whether 

it was wise to begin with a subfile of those 

with 3% years of data, suggesting instead 

starting with an entering cohort and examining it over a six-month period. Reiss 

suggested that there will be sufficient multiple victimization within a six-month 

period to allow the kind of analysis 

Fienberg had proposed for the longer 

records. The suggested advantages of the 

entering cohort approach are that it avoids 

gaps in records (which Fienberg had noted 

as a complication facing his approach) and 

it significantly reduces problems associated 

with panel attrition. And, of course, the 

number of possible patterns is substantially 

smaller with 12 months than with 42 

months. 

Fienberg's answer was that time heterogeneity was more likely to be discoverable 

with the longer records. The conferees then 

suggested starting with entering cohorts 

and "aging" them. It is clear that if they are 

aged far enough, with movers deleted, it 

makes no difference whether one starts 

with entering cohorts and works forward 

or starts with completely aged cohorts: the 

same records are included. And starting in 

either place one might compare different 

cohorts at similar points in their "life cycles" in the panel to investigate stationarity 

of victimization apart from the question of 

time homogeneity Fienberg discussed. The 

question separating the two approaches, 

then, is how long a record is necessary to 

investigate time homogeneity. That, however, cannot be answered a priori. In the 

absence of adequate prior investigations, 

the only way to know whether it is 

necessary to use Fienberg's approach as 

compared with relying upon shorter 

records is to compare findings based on the 

longest possible records with those based 

on shorter ones. 

The discussion of the two possible starting 

points for the investigation Fienberg proposed pointed once again to the problem of 

panel attrition. It has already been noted 

that those with high victimization are relatively likely to move from the household 

location and therefore be lost to the panel. 

There are at least three different reasons for 

this. First, high victimization and household propensity to move may independently be related to other causal variables, 

such as low income. Second, it seems plausible that some households may move 

because of high victimization. Presumably 

in .such cases the household has decided 

there is location proneness. Third, the 

young are relatively likely to leave the 

household, going off to college or setting 

up their own households. Since the young 

have relatively high victimization rates, 

this process will reduce the victimization 

rates for the household considered as a collection of individuals. Either starting point 

for the Fienberg investigation will, provided it ultimately deals with complete long 

records, lead to an examination of a limited 

subset of the original panels, and the victimization experience of the movers is 

likely to differ systematically from the experience of those who remain. Furthermore, if, as is sometimes the case, it is impossible to tell from the data records 

whether the occupants of a household have 

changed from interview to interview, some 

of the "complete" long records will actually 

be spliced records of more than one household (in the nonlocational sense). Given the 

likelihood that the victimization experiences of the various households comprising 

the spliced record will systematically differ, 

these "completed" records will provide 

misleading information. 

While the presentations and discussion at 

the conference focused on questions of 

multiple victimization, they pointed to several important problems in the design and 

analysis of victimization surveys which 

have bearing well beyond questions of multiple victimization. The overriding problem 

is that longitudinal analysis is required, 

while the attention of LEAA and the Bureau of the Census has been directed almost 

entirely to cross-sectional analysis. Related 

to this are several problems resulting from 

selective attrition of panels, largely caused 

by residential mobility and changes in 

family composition. Alteration in survey 

design is required to (1) provide information about the continuity of respondents 

within household locations, and (2) allow 

investigation of patterns of movers, preand post-move. 

Conferees commented upon the Census 

Bureau's "Description of Activities," a 

proposed research agenda for fiscal years 

1978 through 1982. This Description treats 

the matters mentioned in the previous 

paragraph, and it is worth quoting the 

entire treatment: 

3. Quesrionnaire design research 

Research on the most effective questionnaire 

design will focus on the following areas: ... 

d. A method of identifying respondents so they can be traced across time. ... 12. Conceptual issues regarding NCS 

. . . b. Mover/Nonmover Study (including a comparison of in-migrants with out-migrants). 

13. Analyrical issues 

... a. Longitudinal studies. An exploration of 

techniques and difficulties of exploiting NCS 

crime features to do longitudinal analyses. 

It is noteworthy that mention of the longitudinal features of the design and their importance for analysis does not appear until 

the final page of the document. It was the 

clear sense of the conferees both that the 

placement of that brief discussion at the 

end indicated the priority attached to longitudinal analysis by those responsible for 

NCS, and that such low priority was totally 

inappropriate. 

Decisionmaking 

Considerable attention at the workshop 

had been given to aspects of decisionmaking in parole and sentencing. Several 

of the workshop participants continued research in this area and presented results to 

the conference. 

The Salient Factor Score system used by 

the Federal Board of Parole approaches 

the parole prediction problem by assigning 

scores for each individual on nine categorical variables and adding the scores (equally 
weighted) to produce a single Salient Factor Score, which is used to predict parole 

outcome. Herbert Solomon (1976) reanalyzed the data earlier used to develop the 

Salient Factor Score system. He showed 

that, for a subset of four predictor variables, logit models, which weight the variables unequally, can achieve better prediction 

than the equal weighting of the Salient 

Factor Score system, in the sense of fitting 

the observed proportion of successes. (In 

part, no doubt, this better prediction 

occurs because Solomon's method produces a larger number of prediction categories than the Salient Factor system, 

given the same number of predictor 

variables.) Kinley Larntz felt that analysis 

could be pushed further (or at least beyond 

the published description of Solomon's 

work) and that it would be useful to approach a different data base with the same 

general questions. He described his work 

on this problem at the conference. 

The State of Minnesota had undertaken a 

parole project similar to the federal effort, 

developing its own salient factor score system on the basis of an extensive body of 

data concerning released prisoners. Larntz 

obtained data for about 1000 released prisoners from the State of Minnesota, the 

data used in the development of the salient 

factor system, and reanalyzed it using multivariate log-linear methods. (Tables and 

graphs from Larntz's analysis are in his 

"Linear Logistic Models for the Parole 

Decisionmaking Problem.") 

Larntz begins with a logit analysis using the 

eight categorical variables of the salient 

factor scores applied to 485 cases selected 

from the full file (this reduced sample is the 

"construction sample"). This analysis parallels that of Solomon, except for the larger 

number of variables. In addition, Larntz 

tested for two-factor interactions (which 

Solomon does not report having done). 

Only an age at first conviction-burglary 

interaction seemed to have much effect, 

with those first convicted at higher ages 

more likely to be parole failures if qhe 

instant offense is burglary, while whether 

the instant offense is burglary matters little 

for those first convicted at age 19 or 

younger. Larntz estimated models using 

the full eight variables, the,eight variables 

with the one interaction, a subset of four 

variables (equivalent to the Solomon 

model), and four variables with the 

interaction, computing three kinds of chisquared statistics for each. In addition, he 

computed the likelihood ratio chi-squared 

for an equally weighted model ("Burgess 

scale," the salient factor method). While 

models which include the interaction term 

do better than models which do not, 

differences in goodness of fit among the 

various models without the interaction 

term are exceedingly small. That is, it does 

not seem to matter much whether one uses 

four or eight variables (presumably because 

of high collinearity among the variables). 

Nor does it seem to matter much whether 

one uses the equal weights of the salient 

factor method or a more sophisticated 

weighting scheme. 

Larntz then removed the restriction of the 

analysis to categorical variables. Several of 

the categorical variables of the first analysis were produced by categorizing measured 

scales, and Larntz therefore restored the 

original scales. Removing the restriction 

called for changing the analysis technique 

to logistic regression, and Larntz applied 

this technique to seven variables which are 

quite similar to the variables used in the 

earlier analysis. See Larntz, for partial 

results. Once again, the number of variables included in the model did not have a 

striking effect on goodness of fit. Indeed, a 

model containing only two variables, age at 

first conviction and number of previous 

parole failures, performed nearly as well as 

a seven-variable model. Larntz tested interactions, but did not include any in the 

reported models because they seemed to 

have little effect. It is striking that even the 

seven-variable model does not represent an 

enormous increase in goodness of fit overa 

model using no variables except a constant 

term. It is difficult to compare the logistic 

regressions with the logit models in terms 

of goodness of fit, since the variables used 

in the logit models were selected by the 

Minnesota parole project precisely because 

they produced a salient factor score which 

seemed to "work" well for the data Larntz 

was using. The variables used in the logistic 

regressions were somewhat less preselected. 

The point of parole prediction models, of 

course, is not to fit observed probabilities 

of parole failure for categories of potential 

parolees. It is rather to provide predictions 

of success or failure which may serve as the 

basis for parole decisions. The important 

question, therefore, is how well the model 

is able to separate parole successes from 

parole failures. Larntz turned to the other 

half of the data set, the validation sample, 

for an approach to this question. The logic 

is roughly as follows. For each individual 

in the sample, the model will generate a 

prediction of success. The analyst then 

chooses a cutpoint on the probability scale. 

The group of individuals with predicted 

probabilities above the cutpoint will presumably include some parole failures and 

some parole successes. The group below 

the cutpoint wil! also include some successes and some failures. The difference 

between the proportion of all successes 

who fall above the cutpoint and the proportion of all failures who fall above the 

cutpoint is a measure of the ability of the 

model to discriminate properly. As the cutpoint is varied, this difference is likely to 

change, and the proportion of the whole 

group falling above the cutpoint will surely 

change. For each of the models Larntz 

varied the cutoff point and examined the 

key difference. These results are presented 

as a series of graphs. To facilitate comparison across models, Larntz graphed the differences not as functions of the cutoff 

point, but rather of the proportion of the 

total sample below the cutoff point. 

It is to be expected that the logistic models 

will perform relatively well in this test, because the variables had initially been 

selected on the basis of their performance 

in the combined validation and construction samples. Performance of the logistic 

regressions near this level would, because 

less preselection of variables was involved, 

indicate that they are of a relatively high 

quality. The high peak associated with a 

logistic regression based on only two 

variables is therefore particularly striking. 

In principle, analysis of this kind could be 

used to select an optimal cutpoint value. 

However, that selection depends upon 

criteria for optimality, and it is not entirely 

clear what those criteria should be. Maximum separation is obviously an attractive 

candidate. However, one might want to, 

say, sacrifice some degree of separation for 

a larger proportion of the total sample 

below the cutpoint. 

Larntz next asked whether the effects of 

preselection of variables distorted the 

results, so that the estimated probabilities 

were in fact not very good estimates. He 

tested this possibility by taking the estimated probabilities from each model and 

using them to generate a binomial random 

variable (success or failure) for each individual. He then repeated the cutpoint and 

difference analysis for each model, using 
the generated outcome scores rather than 

the actual outcomes. Graphs for three 

models are presented in Larntz. The first 

two graphs are for logistic models. It is 

clear that in both czses the curve has shifted 

upwards, which suggests that the distribution of estimated probabilities is too spread 

out. Application of these models to a new 

data set should reveal considerable shrinkage. There is noticeably less upward 

shifting for the one logistic regression 

model included, indicating that the estimated probabilities are reasonably good. 

And it should be emphasized that the 

logistic regression involved here has only 

two predictor variables. The conclusion is 

that a very simple model, involving only 

two variables, performs quite satisfactorily-at least in comparison with the other 

models tested. It is obvious, however, that 

there remains considerable error in prediction. 

Howard Wainer has also worked on the 

parole prediction problem, using data from 

the Federal parole system. Since his 

attempts to improve upon the predictive 

performance of the salient factor system by 

use of alternative estimation procedures 

had earlier been considered by most of the 

conferees, they were not discussed extensively at the conference. But it is worth 

mentioning that, by using psychometric 

methods applied to the variables used in 

the Federal salient factor scores, Wainer 

was able to improve on the salient factor 

score predictions. However, as with 

Larntz's various models, the improvement 

in predictive power was relatively small, 

and the resulting predictions are not very 

accurate. As Wainer and Perline have written, "our results are at least as good with 

this approach as with any other, but still 

leave a great deal to be desired." 

The conferees were in general agreement as 

to why none of the approaches leads to very 

good prediction of parole success or 

failure. Leaving aside such common problems of prediction as, say, the influence of 

chance events on behavior, there is the 

problem that the parole prediction problem is considered only in the context of a 

highly homogeneous population representing a very small and extreme portion of the 

distribution of behavioral characteristics. 

The prison population is itself extremely 

restricted in its range of variation, and presumably an extreme portion of the prison 

population is seen as "obviously" unsuitable for parole, so the parole data base is 

even more restricted. As Leslie Wilkins put 

it, parole prediction is an attempt to predict 

far out in the tail of a distribution, which is 

a difficult thing to do. It is therefore not 

surprising that it appears difficult to improve upon Larntz's two-variable logistic 

regression model. 

Wainer in fact told the conferees that he 

had given up hope of accurately predicting 

recidivism (or parole failure), and in his 

work on what appeared to be the parole 

prediction problem was actually addressing a different question. From the perspective of his analytic approach, events (or the 

variables involved in parole prediction) are 

viewed much like items in a test, and each 

event is characterized by its "rarity" ("difficulty" in the testing context). Recidivism, 

or parole failure, is viewed simply as an 

event with a certain amount of rarity. Individuals in the testing context are characterized by their level of ability, which, in 

the parole context, Wainer refers to as 

"probity." The statistical methods yield 

estimates both of the rarity of events and of 

the probity of individuals. 

Wainer wants to beable todescribe institutions, say in the criminal justice system, by 

the characteristics of the individuals entering them. Then, if one saw that recidivism 

among the products of some institution 

were declining, one could ask whether the 

decline resulted from a change in the nature 

of the institutional population or from 

something else, such as a new program 

which had been instituted. In other words, 

one would want to examine recidivism of 

the institutional population controlling for 

the probity of the population. The focus, 

then, .is shifted from prediction of 

individual behavior to system characteristics. 

Having introduced this perspective to the 

conferees, Wainer presented a problem for 

their consideration. In estimating rarity 

and probity, he has found occasional itemperson interactions, or instances in which 

particular item-person combinations are 

badly fit by the model. The analogy in the 

testing context is to those occasions on 

which an individual with low ability nevertheless gets a difficult item right, or an individual with a high ability misses an easy 

item. Because of the probabilistic nature of 

the event-person combinations, some 

"errors" of this kind are bound to happen. 

However, they seem to happen more often 

than the probability model would suggest. 

Furthermore, even if they are expected to 

happen, they cause difficulty for the estimation of individual probity, particularly 

if the item is far from the individual's probity, because information about individual 

probity decreases with distance of the item 

from the individual probity while its influence on the estimate of probity increases. The problem, then, is how to 

reduce or eliminate the effects of these 

errors in estimating probity. 

The statisticians at the conference discussed 

this estimation problem at some length, 

providing Wainer with some useful suggestions, but not reaching a clear solution. 

While predictions of success are important 

in modern methods of parole decisionmaking, they are not the sole basis for the 

decision. The Federal probation guidelines 

combine salient factor scores (i.e., predictions) with offense characteristics ("seriousness'') to produce "average total time 

served before release. " Wainer applied 

two-way table decomposition methods to 

the matrix showing the midpoints of recommended sentence intervals for each 

combination of salient factor score and 

offense characteristic category in the 

salient factor system. His results indicate 

that "the existing parole policy corresponds 

closely to a multiplicative model in which 

seriousness of offense seems to count 

almost three times as much as offender 

characteristics among adults" (Perline and 

Wainer). The relativeIy small effect of the 

salient factor scores (that is, the measure of 

offender characteristics or of probability of 

recidivism) suggests either that the inaccuracy of the predictions of recidivism is 

taken into account in decisonmaking, or 

that characteristics of the offense are 

considered more important in determining 

time served. Wainer suggests that the two 

dimensions of the guideline scheme, salient 

factor scores and offense characteristics, 

correspond to two schools of thought on 

incarceration, rehabilitation, and retribution. It could be argued, then, that his 

finding concerning the relative importance 

of the two factors indicates the relative 

importance of the two views of the purpose 

of incarceration in parole decisionmaking. 

Before parole boards can consider the decision to release a prisoner, there must be a 

decision to incarcerate the individual in the 

first place. David Britt and Kinley Larntz 

have investigated judicial sentencing decisions, using a sample of 200 cases from the 

Denver, Colorado, courts, originally collected under the auspices of the State 
Courts Sentencing Project and provided by 

Leslie Wilkins. After elimination of cases 

because of inadequate data or because they 

involved "victimless crimes," 138 cases 

were analyzed to determine the major factors used by judges in reaching thedecision 

of whether or not to incarcerate an individual convicted of a criminal offense. Logit 

models were used in the analysis. 

In brief summary, the results indicate that 

dispositions of crimes against property 

appear related to variation in the seriousness of the crime and the offender's previous record in a straightforward way. "As 

the crime becomes more serious and the 

offender's previous record becomes poorer, 

the chances of the individual's being incarcerated increase." (Britt and Larntz). 

Furthermore, seriousness of offense does 

not seem to lead to incarceration for those 

with a good prior record. For crimes 

against persons, seriousness of offense did 

not play a large role in incarceration, presumably because nearly all the offenses 

involved were relatively serious ones. A 

two-variable model using the nature of the 

plea and whether the charge was reduced 

best fit the data. No characteristics of the 

offender affected the chances of being 

jailed once these two variables were taken 

into account. 

The contrast between sentencing decisions, 

at least as they appear to be made in Denver, and parole decisions under modern 

guideline systems is worth noting. The 

parole decision system explicitly builds in a 

variety of characteristics of the individual 

in determining release. The sentencing 

decisions incorporate no individual characteristics (but for prior record in the case 

of property offenses) in determining when 

to incarcerate. 

Several qualifications should be introduced. First, the sentencing study did not 

investigate length of sentence. Second, individual characteristics may be incorporated into prior events in the criminal justice system: the Denver data concern only 

convicted individuals. Individual characteristics may play a far larger role in the 

decisions to arrest, prosecute, and convict. 

A full investigation of the various factors 

determining outcomes in the criminal 

justice process would have to begin at a 

much earlier stage than the sentencing 

stage. It seems likely that the development 

of OBTS data will make such investigations 

easier to conduct in the future. 

Deterrence 

The problem of estimating the deterrent 

effect of criminal sanctions occupied considerable time at the workshop and considerable effort by workshop participants 

since then. The major work on deterrence 

since the workshop has been that of the National Research Council's Panel on Research on Deterrent and Incapacitative 

Effects (1978). The panel was chaired by 

workshop participant Alfred Blumstein 

and included two other workshop participants, Gary Koch and Albert J. Reiss, Jr. 

Daniel Nagin, staff to the panel, spent several weeks at the workshop, and Brian 

Forst, co-author of one of the panel's commissioned papers, reported on his research 

to the workshop. It is appropriate, therefore, that the conference discussion of deterrence began with a brief statement by 

Blumstein summarizing the panel's work. 

Blumstein noted that the panel had focused 

on general deterrence, where the issue is the 

association between crime rates and sanctions. Virtually all the research on this issue 

has found, after controlling for other 

determinants of crime, a negative association between crime and sanctions. Whether 

there is a causal relationship is a more difficult question. The panel considered three 

principal aspects of this question: 

1. Single equation models typically use, on 

the left-hand side of the equation, a fraction in which crime is the numerator, while 

the sanction risk on the right-hand side of 

the equation is a fraction with crime in the 

denominator. If there is error in the measurement of crime, it will generate a negative 

association between crime rate and sanction risk, even in the absence of a deterrent 

effect. Without good estimates of the magnitude of the error, therefore, it is difficult 

to know what to make of the association 

found in the data. 

2. Imprisonment is typically the sanction 

used in deterrence studies. However, while 

the risk of imprisonment may have a deterrent effect, the fact of imprisonment may 

affect crime rates through kcapacitation of 

active criminals. An estimated effect of imprisonment, therefore, may combine both 

deterrent and incapacitative effects in unknown proportions. 

3. A negative association between crime 

and sanction may result from deterrence of 

crime by sanction, but it may also result 

from the inhibition of sanction by rising 

crime rates. This is particularly a problem 

in studies which, like most published 

studies of deterrence, rely on crosssectional data at the state level. It is also a 

particular problem to the extent that studies rely on the sanction of imprisonment, 

because it is reasonable to suppose that imprisonment decisions are influenced by 

such factors as prison crowding. If imprisonment rates and crime rates are simultaneously determined, as this suggests, then 

simultaneous equations models may become appropriate. Estimation of simultaneous equations models requires appropriate identification restrictions, that is, 

variables which influence sanctions but not 

crimes, or variables which influence crime 

but not sanction risk. The choice of identifying restrictions is a difficult problem, 

which, in the panel's view, has not been 

adequately resolved. 

In sum, a deterrent effect is not clearly 

demonstrated in existing studies. This brief 

presentation sparked considerable discussion among the conferees. A number of 

them argued that treatment of the simultaneity problem involves far more than 

choosing appropriate identifying restrictions and separating deterrence and incapacitation. The argument is that the relationship between imprisonment and crime 

rates is more complicated than the aggregate statistical models suggest. The ways in 

which adaptation to the pressures of 

changing crime rates affects prisons over 

time, and the related question of how 

changes in prisons affect crime rates, have 

not been studied to any substantial extent. 

The composition of prison populations 

may shift, the social environment of the 

prisons may change (arguably making prisons more-or less-attractive places to 

be), the symbolic meaning of imprisonment may change as prisons become politicized, and so forth. Further, it is 

reasonable to expect that the effects of 

imprisonment on crime rates depend upon 

prison release rates and the character of the 

prisoners released. At the very least, disentangling these factors requires disaggregation of the available data by offense-a 

recommendation with which the panel 

agrees and which is followed in a number of 

the studies. Whether modifications to 

account for the other problems and questions can be built into the kind of aggregate 

analysis common in the study of deterrence 

is another matter. In any event, the requisite data are not available to do so now 

even if in principle it can bedone. The question of whether valid conclusions about the 

deterrent effect of sanctions can be reached 

through the use of aggregate models which 

do not include these complex problems was 

not resolved in conference discussion. 
Discussion then turned to the problem of 

estimating deterrent effects in single equation models. Blumstein had noted that if 

crime is measured with error in the standard models for the problem, estimates of 

deterrent effects are biased. The standard 

model would take the following form: 

Where C = number of crimes 

N = population 

I = number of sanctions 

e = random error term 

A = parameter to be estimated 

Estimates of A are biased if Cis measured 

with error. Blumstein added, however, that 

if C is measured without error, then unbiased estimates of A are possible. The 

statement generated considerable controversy, less because conferees believed it to 

be false (it is not clear that any of them felt 

it was false, when properly qualified) than 

because its implications for the study of deterrence are problematic. In other words, 

presuming an unbiased estimate of A, is 

that estimate a measure of the deterrent 

effect of criminal sanctions? The question 

can be approached through two hypothetical experiments, the first proposed by 

Blumstein and the second by other conferees. 

Blumstein's experiment is roughly this. 

Pick a value for A. Generate data for Iand 

C, without error. (These may be real or 

hypothetical data.) Generate a random 

variable e. Then use the equation to generate values of C/ N. Label I/C "imprisonment rate" and C/ N (as generated by the 

model) "crime rate." Give these variables to 

a statistician and ask him to estimate A. 

The statistician should be able to produce 

an unbiased estimate of (the known value 

of) A. The structure of the model suggests 

that A is a measure of the effect of the imprisonment rate on the crime rate. 

The second experiment uses a random 

number generator to produce values for C, 

I,and N. Then the two variables C/ N and 

I/C are formed. The correlation between 

them is calculated. Given the construction 

of the variables, there should be a negative 

correlation, even though number of crimes, 

number of incarcerations, and population 

are random numbers. In other words, 

Blumstein's statistician, given "crime rate" 

and "incarceration rate" and asked to estimate (the unknown value of) A, will produce an estimated negative value. Since the 

data are purely random, it is difficult to see 

why A should be considered a measure of 

the deterrent effect of incarceration. 

In objecting to Blumstein's hypothetical 

experiment, conferees noted that by fixing 

values of Cand using them in the model to 

generate values of C/ N, the experimenter 

would in effect be generating simply values 

of the reciprocal of N. This suggested to 

some of the conferees that the problem was 

incorrectly formulated. As one conferee 

said, "You cannot fix Cand then talkabout 

generating crime rates." 

Another approach to the question formulates the basic equation in terms not of the 

quantities actually used in the standard 

approaches, but rather in conceptual 

terms. Thus "crime rate,"or something like 

it, is seen as a function of "sanction risk," 

among other things. Call the coefficient of 

"sanction risk" B. Then the standard equation is seen as a particular realization of the 

conceptual model, using proxies for the 

conceptual variables. Then there are two 

separate questions which can be asked of 

the estimation. First, is the estimate of A 

unbiased? That question, which has 

apparently preoccupied the literature, 

appears to have the answer Blumstein suggested: if C is measured without error, an 

unbiased estimate of A is possible. The 

second question, however, concerns the 

relationship between A and B. And it 

would appear that the particular structure 

of the variables used in the estimationthat is, the presence in the denominator of 

the sanction risk variable of the numerator 

of the crime rate variable-means that A is 

not an unbiased estimate of B. 

If the answer to the second question suggested above is correct, it immediately 

raises another problem. How does one estimate B? Colin Loftin, drawing upon his 

own deterrence research, suggests using 

sanctions rather than sanction risk as the 

explanatory variable. He noted that the 

deterrence research has generally found 

that measures of theseverity of punishment 

have less of an effect on crime rates than do 

measures of the certainty of punishment. 

Severity measures, unlike certainty ("risk") 

measures, do not share a common element 

with crime rate measures. Loftin has used 

number of executions as a sanction 

variable in his capital punishment research. 

This removes the common term, but it 

leaves somewhat open the question of the 

underlying behavioral model. 

A strong theme of much of the discussion 

of this problem was that the specification 

of deterrence models common in the literature may not allow thedetermination of deterrence effects. Considerable complexity 

must be added to the models. The "crime 

rate" needs to be decomposed. It might be 

viewed as a function of a distribution of individual rates of offending. As Reiss has 

written, "there are three general kinds of 

change that affect the incidence of crime in 

a population. They are changes in the 

prevalence of offenders in a population, 

changes in individual incidence of offending, and inferactions between prevalence 

and incidence rates" ("Understanding 

Changes in Crime Rates''). In effect, thelefthand side of the deterrence equation must 

consider all of these. Both prevalence of 

offenders and individual rates of offending 

may be influenced by the criminal justice 

system in a number of ways, and these 

would need to be considered on the righthand side. In addition to the general 

deterrent effect of imprisonment, one 

should consider the incapacitation effect, 

the effects of differential release rates, and 

other complications. In the opinion of 

some of the conferees, unless decompositions of this sort are essayed, it will be impossible to disentangle the various effects 

of sanctions and therefore impossible to 

estimate a deterrent effect. Analysis along 

these lines, however, is not a short-term 

project. The data simply do not now exist 

to implement it. 

There remains the possibility that, short of 

implementing the more complex model 

described above, one can consider estimates derived from the standard deterrence model as measures of the aggregate 

effect of sanction risk, without worrying 

too much about what proportion, if any, of 

the aggregate effect is actually deterrence. 

Taking that approach raises the question of 

whether the findings of deterrence research 

can be accepted, subject to this rather substantial limitation. 

Stephen Fienberg has taken a close look at 

some of the deterrence studies, and the 

results he reported to the conference suggest that estimates of the deterrent effects 

of sanctions should be treated with some 

caution. (Fienberg subsequently supplied a 

written version of his report, Brier and 

Fienberg, "Recent Econometric Modelling 

of Crime and Punishment: Support for the 

Deterrence Hypothesis?".) 

Fienberg first examined lsaac Ehrlich's 

(1973) well-known analysis of 1960 data 

from 47 states and the reanalysis of these 

data done by Vandaele (1978) for the National Academy panel. Fienberg first notes 
the well-known shortcomings of Uniform 

Crime Re~orts data as measures of the 

variables ;equired by Ehrlich's supply of 

offenses function and suggests that it 

would be appropriate to use statisticai 

methods designed for the "errors in variables" problem and for multiple indicators 

of unobservable variables. Ehrlich's 1960 

data were unavailable and published reports do not fully specify the simultaneous 

equations model actually used, so it was 

not possible to replicate the Ehrlich analysis. Vandaele had reanalyzed the Ehrlich 

data and concluded that inferences about 

deterrence are not sensitive to changes in 

the specification of the model. Using the 

data reported by Vandaele, Fienberg was 

able to duplicate the results. However, he 

questions the conclusion that inferences 

are not sensitive to changes in specification, noting that Vandaele's published results for murder, rape, and assault do seem 

sensitive to the choice of specification. This 

is no small problem, because the correct 

specification cannot be. determined by 

analysis of the data themselves. 

One of the kev variables in the analvsis is 

probability of incarceration, measured by 

the ratio of the number of commitments to 

the number of offenses. Vandaele had 

noted that for several states this ratio is 

greater than one, which, of course, is the 

upper limit for probabilities. This is not 

necessarily an indication of error in the 

data, because there are a number of plausible and reasonable explanations for ratios 

greater than one. It does, however, suggest 

that the ratio may not be a reasonable measure of the perceived probability of incarceration. Vandaele reestimated the equations deleting states with ratios greater 

than one and found little change in the 

results. Fienberg argues that to treat the 

data in this way is to assume that, while 

ratios greater than one may be bad data, 

there is nothing wrong with ratios less than 

one. However, Fienberg continues, the fact 

that the underlying process produces probability estimates greater than one suggests 

that there is something very wrong in the 

process as a whole, and therefore that there 

is no more reason to accept ratios less than 

one than to accept those greater than one. 

Using an analogy, he suggests that if a computer program computes 100 correlations, 

and 5 of them have values greater than 1.O, 

wisdom may dictate throwing out all 100 

values, and not just the 5 impermissible 

ones. The impermissible values serve as evidence that none of the values are to be 

trusted. Fienberg's logic strongly suggests 

the conclusion that no deterrence studies 

relying upon such data can be accepted as 

providing reliable evidence of a deterrent 

effect. 

Brian Forst (1976) attempted to replicate 

Ehrlich's study using 1970 data. There are 

differences in some of the variables used by 

Forst and Ehrlich, and Forst did not follow 

EhriichS specifications. in particular, 

Forst used more sociodemographic variables than Ehrlich. Further, Forst analyzed 

only the aggregate crime rate, while Ehrlich 

used rates for individual crimes. Forst's results differ strikingly from those of Ehrlich, 

as he found the coefficients of the deterrence variables insignificant. It is, of 

course, possible that these differences are 

to be explained by a change in patterns of 

criminal behavior over a 10-year period, 

but it is not clear what would explain such 

a change. The extra sociodemographic 

variables may also explain the difference. 

Fienberg obtained most of the Forst data 

and reanalyzed it. He was able to duplicate 

Forst's results quite closely. However, one 

key variable, a measure of income dispersion, could not be obtained from Forst, 

and Fienberg therefore used several 

different measures of income dispersion. 

He discovered that the choice of a measure 

had substantial effects on most of the 

estimated coefficients. That is, the model is 

extremely sensitive to minor differences in 

the definition of a single variable. Since 

there are no strong grounds for preferring 

one definition to another, this suggests 

extreme caution in accepting the results of 

the analysis of deterrence effects. 

One of the most widely discussed deterrence studies is Ehrlich's (1975) longitudinal study of the deterrent effect of capital 

punishment. Ehrlich's data could not be 

obtained, and Fienberg therefore reanalyzed the closely related data of Bowers and 

Pierce. While Fienberg discusses a number 

of methodological problems which raise 

questions about Ehrlich's specifications 

and conclusions, only two aspects of the reanalysis will be discussed here. 

The Ehrlich data cover the years 1933-1969, 

and, because of the use of lags, analysis is 

limited to 1934-1969. Other analysts have 

noted that if the years 1963-1969 are 

deleted, the coefficient of the probability of 

execution variable loses statistical significance. To this Fienberg adds two points. 

First, by redesigning aspects of the analysis, so that the model was recursive, not 

simultaneous, he was able to analyze residuals, and these analyses show that the 

observations for 1963-1969 are discrepant. 

This reinforces the argument of other 

analysts that the relationship among the 

variables has changed over time, so that it 

is misleading to compute the deterrent 

effect based on the entire series. Second, 

analysis of residuals points to 1934 as an 

outlier in the data. Deleting that one 

observation has a substantial impact on the 

estimated coefficients. In the original scale 

of the variables, the coefficient of the 

execution variable is negative but not 

statistically significant. In a logarithmic 

specification, the estimated coefficient is 

positive. The data for 1934 show a small 

value for the murder rate and a high value 

for the execution variable (number of 

executions for murder in year t + 1 divided 

by the number of convictions in year t). 

Fienberg suggests that the 1934 data are 

"suspect." Whatever the explanation, the 

fact that a single observation has such a 

substantial effect on the estimates reduces 

confidence in the findings generally. 

Ehrlich's specification of the "murder supply" function is linear in logarithms, with 

one major exception. Time, used as a surrogate for improvements in medical technology, enters the transformed equation 

(that is, the equation after converting to 

linearity in the logarithms) untransformed. 

The reason for treating time differently 

from all the other variables is not clear. 

Fienberg reestimated the murder supply 

function using a fully logarithmic specification (that is, using logT instead of T). The 

effect was to change the sign of the coefficient of the execution variable. Fienberg 

then tried various other transformations of 

time and discovered that by this means he 

could change the results of the estimation 

almost at will. This might not be a great 

problem if there were some logical defense 

for the choice of any particular transformation, but none is apparent. Stated in very 

strong form, the appropriate conclusion 

would appear to be that longitudinal analysis of the Ehrlich capital punishment data 

can produce virtually any conclusion about 

the deterrent effect of capital punishment, 

depending upon the arbitrary choice of a 

scale for time. 

The final paragraph of the Brier-Fienberg 

paper baldly presents their overall conclusions: "We can find no reliable empirical 

support in the existing literature either for 

or against the deterrence hypothesis. 

Moreover, we believe that little will come 

from further attempts to model the effects 

of punishment on crime using the type of 

data we have described in this paper." This 

reinforces the lessons suggested above: a 

reformulation of the problem must precede 

any advances in the study of deterrence. 
Ehrlich, lsaac (1975) . "The deterrent effect of capital punishment: A 

question of life and death." American Economic 

Review 65:397-417. 

Ehrlich, lsaac (1973) 

"Participation in illegitimate activities: A 

theoretical and empirical investigation." Journal 

of Political Economy 81521 -565. 

Forst, Brian E. (1976) 

"Participation in illegitimate activities: Further empirical findings." Policy Analysis 2477-

492. 

National Research Council (1978) 

Deterrence and incapacitation. (Panel on Research on Deterrent and lncapacitative Effects.) 

Edited by Alfred Blumstein, Jacqueline Cohen, 

and Daniel Nagin. Washington, D.C.: National 

Academy of Sciences. 

Solomon, Herbert (1976) 

"Parole outcome." Journal of Research in 

Crime and Delinquency, July, 107-126. 

Vandaele, Walter (1978) 

"Participation in illegitimate activities: Ehrlich revisited." In National Research Council, 

Deterrence and incapacitation, Washington, 

D.C.: National Academy of Sciences. 

Conference participants 

Alfred Blumstein 

Urban Systems Institute 

Carnegie-Mellon University 

David W. Britt 

Criminal Justice Program 

Nova University 

Stephen E. Fienberg 

Department of Statistics 

and Department of Social Science 

Carnegie-Mellon University 

Kinley Larntz 

Department of Applied Statistics 

University of Minnesota 

Colin Loftin 

Department of Sociology and 

Center for Research on Social Organization 

University of Michigan 

Albert J. Reiss, Jr. 

Department of Sociology 

Yale University 

Richard F. Sparks 

School of Criminal Justice 

Rutgers University 

Howard Wainer 

Bureau of Social Science Research 

Washington, D.C. 

Leslie T. Wilkins 

School of Criminal Justice 

SUNY at Albany 

Guests 

Charles R. Kindermann 

Bureau of Justice Statistics 

U.S. Department of Justice 

Paul D. White 

Bureau of Justice Statistics 

U.S. Department of Justice 

staff 

David Seidman 

Social Science Research Council 

Center for Coordination of Research on 

Social Indicators 

Conference papers and other materials 

Brier, Stephen S. and Stephen E. Fienberg 

Recent econometric modelling of crime and 

punishment: Support for the deterrence hypothesis? 

Fienberg, Stephen E. 

Victimization and the National Crime Survey: 

Problems of design and analysis 

Larntz, Kinley and David W. Britt 

The effects of plea bargaining on the disposition of person and property crimes: A research 

note 

Larntz, Kinley 

Linear logistic models for the parole decisionmaking problem 

Loftin, Colin 

Alternative estimates of the impact of certainty and severity of punishment on levels of 

homicide in American states 

Reiss, Albert J., Jr. 

Understanding changes in crime rates 

Reiss, Albert J., Jr. 

Victim proneness by type of crime victimization over time 

Sparks, Richard F. 

Criminal opportunities and crime rates 

Wainer, Howard and Richard Perline 

Quantitative approaches to the study of 

parole 
-- - 

Criine rates and victimization 


Understanding changes in crime rates 


ALBERT3. REISS,JR . Department of Sociology 

Yale University 

Much of the empirical research in criminology is based on. explaining changes in 

crime rates and much of the research evaluating law enforcement or criminal justice 

programs depends upon measuring changes 

in crime rates. The choice of measures of 

crime is much debated and their validity or 

reliability critically reported. Yet the relationship among measures of crime, e.g., between crime incident rates and aggregate 

rates of individual offending, is not well articulated. This stems in part from a lack of 

understanding of the nature of crime 

events, of the criteria for selecting measures 

based on such events, and of the sources of 

change in measures of crime. This paper 

attempts to clarify some of these problems 

in the measurement of crime using examples primarily from research on deterrence 

and incapacitation. 

Understanding crime events 

Any occurrence of crime is a complex 

event. Scanting most elements in the occurrence of crime events, the three critical ones 

for measuring crime are that an event may 

comprise one or more criminal acts, one or 

more offenders, and one or more victims. 

Of less critical significance are variation in 

duration of events in time and the number 

of settings involved in the criminal activity. 

Now it is commonly understood that when 

a crime event is counted as a single crime 

act or incident, the number of victims and 

of offenders on the average exceed the 

number of crime incidents since some 

events involve more than one victim 

and/or more than one offender. But what 

often is overlooked is that when there is 

more than one offender for any incident, 

the offenders acdount for only a single 

crime event (even though the police understand that multiple arrests for a single 

incident clear osly that incident, barring 

admissions by the offenders to other crime 

events). 

Likewise, where there is more than one 

offender and more than one criminal act in 

an event, different offenders may commit 

different acts in that event. While these differences may be reflected in different 

charges or indictments for offenders involved in a common event, they will not be 

reflected in measures that assign each 

offender the same crime incident classification. 

We shall not pursue here other implications 

of multiple offenses, offenders, and victims 

in crime events since we shall have occasion 

to draw the reader's attention to some of 

them in presenting a simple model for understanding changes in crime rates. 

Understanding changes 

in crime incident rates 

Whether a crime event is classified as a single incident or as multiple incidents, there 

are three kinds of change that affect the 

incidence of crime in a population. They 

are changes in the prevalence of offenders 

in a population, in individual incidence of 

offending, and in interactions between 

prevalence and incidence rates. Assuming 

no changes in individual incidence of 

offending (or interactions), for example, an 

aggregate crime incident rate may change 

solely due to changes in the prevalence of 

offenders in a population. Correlatively, if 

the prevalence rate remains constant, 

changes in the individual incidence of 

offending will affect the aggregate crime 

incidence rate. Because the prevalence rate 

and the individual incidence of offending 

may vary independently, their rates of 

change may be negatively as well as positively correlated. 

Changes in the prevalence 

of offenders 

Any change in the prevalence of offenders 

in a population comes about as a consequence of changes in replacement rates for 

a population of offenders. Changes in entry 

or exit from a population of offenders or of 

age at onset and desistance from a population affect replacement rates. We may identify several sources of change in replacement rates. 

First, it has long been understood that 

changes in the size ofbirth cohorts or of cohorts at .risk in the population affect the 

prevalence of offenders in a population if 

the probabilities of age at onset and desistance and individual rates of offending 

remain constant. Even when the prevalence 

rate for a cohort remains constant, any increase or decrease in the size of birth 

cohorts affects the prevalence of offenders 

in a total population after the cohort 

reaches the age- of onset of offending. 

Second, while it is understood that changes 

in length of offending career may have an 

effect on the crime rate, it is not generally 

appreciated that both changes in age at 

onset and at desistance can affect the replacement rate of offenders in a population 

and, therefore, the prevalence of offenders 

in a population. 

Third, changes in the number, size, degree 

of openness, composition, and territory of 

social networks may affect the prevalence 

of offenders in a population, since these 

changes affect the potential for recruitment 

of offenders to offending groups. Both 

changes in market networks for the goods 

and services of crime as well as changes in 

formal and informal social networks mav 

affect recruitment. 
These changes are not necessarily independent one of another. Changes in social 

networks, for example, can affect changes 

in the age at onset or desistance from offending. It also is possible that beyond a 

certain point changes in the prevalence rate 

may increase both the number and size of 

social networks, a phenomenon sometimes 

observed in gang delinquency and organized crime. The relationship of processes 

of recruitment to the number and size of 

social networks is not well understood. 

Changes in individual 

offending rates 

Any change in individual incidence of 

offending likewise affects the crime incidence rate. We may think of three major 

types of change that affect individual rates 

of offending in a population. 

First, changes in opportunities to commit 

crime events can change individual rates of 

offending. Assuming an offender, his or 

her probability of offending is some function of both opportunities and intervening 

opportunities to commit criminal acts. The 

opportunity to commit motor vehicle theft, 

for example, may increase both as the ratio 

of motor vehicles to the population increases and as the ease of a successful 

attempt increases. 

Second, changes in the size or structure of 

an offending group or network can alter 

the group and, therefore, an individual 

member's rate of offending. There is plausible evidence that on the average an individual's rate of offending is greater as a member of an offending group than as a lone 

offender. Any reduction in the ratio of 

individual to group offending, therefore, 

should increase, on the average, individual 

rates of offending. 

Third, changes in the size and composition 

of crime networks should affect an individual's rate of offending. Substantial changes 

in markets for illegal goods or services, for 

example, can affect the individual offender 

as an agent of supply, assuming elasticity of 

victims in the population. 

Implications for research on deterrence 

and incapacitation 

Little is known about the distribution of 

individual rates of offending or changes in 

individual rates of offending during an 

offender's career. In particular, almost 

nothing is known about the mix of individual and group offenses in an individual's 

rate of offending. The National Crime Survey of crime victims provides information 

on the number and selected characteristics Unfortunatqy, we do not know how many 

of offenders in crime incidents reported by dfferent offenders are involved in these 

victims. For crimes against persons, the crime incidents reported during a 6-month 

number of offenders is usually reported; period. Nonetheless, when we view these 

for most crimes against property, offenders crime incidents in Table 2 from the per- are not known. Table 1 provides informa- spective of an offending population, we see tion' on the size of offending groups for that only 30 percent of all offenders in these 

selected types of crime incidents while crime incidents were lone offenders. Again, 

Table 2 has information on the distribution there is considerable variation with only 10 

of offenders by size of offending group for percent of all offenders who commit a serithe same types of crime. ous assault with a weapon followed by theft 

Although there is considerable variation in being lone offenders but 58 percent of all 

the individual or group contribution to offenders who commit a rape with no theft 

offending in crime incidents reported by being lone offenders. There is, on the avervictims in Table 1, almost two of every age, 2.1 offenders for each crime incident 

three reported incidents involved only a against a person. There is considerable 

single offender. For crimes against the per- variation in this average with 2.9 offenders 

socn the proportion of incidents committed on the average for incidents of serious 

by a single offender ranged from only 30 assault with a weapon followed by theft to 

percent of all serious assaults with a 1.4 offenders for a rape with no theft. 

weapon followed by theft to 82 percent of 

all attempted rapes with no theft from the 

victim. 

Table 1. 

~otai 

incidents 

Type of crime offenders 

known 

Rape w/theft 30 

Rape, no theft 112 

Att. rape, w/theft 39 

Att. rape, no theft 31 6 

Robbery, w/weapon 752 

Robbery, no weapon 596 

Att. robbery, w/weapon 432 

Att. robbery, no weapon 584 

Ser. assault, theft, weapon 51 9 

Ser. assault, theft, no weapon 71 

Ser. assault, weapon, no theft 1,339 

Ser. assault, no weapon, no theft 244 

Minor assault, theft 485 

Minor assault, no theft 1,947 

kt. assault, w/weapon, no theft 3,289 

Att. assault, no weapon, no theft 5,940 Purse snatch, no force 249 

Att. purse snatch, no force 202 

Pocket picking 441 

Burglary, forced entry, something taken 95 

Burglary, forced entry, 0 taken, damage 126 

Burglary, forced entry, 0 taken, 0 damage 44 

Burglary, unlawful entry, 0 force 588 

Burglary, att. forced entry 374 

Larceny, $250+ 120 

Larceny, $1 00-$249 208 

Larceny, $50-$99 279 

Larceny, $25-$49 302 

Larceny, $1 0-$24 454 

Larceny, under $10 749 

Larceny, $ unknown 103 

Att. larceny 842 

Car theft 74 

Att. car theft 120 

Theft, other vehicle 14 

Att. theft, other vehicle 26 

Total 22,107 

Percent 10e.O 
Given the limitations in these data that we tion by high-rate lone offending persons or individual's crime rate, then it would be 

do not know how many different offenders unless high-rate offending persons who more reasonable to assume that on the 

are involved in the reported incidents (we commit group offenses have a substantial average incapacitation would avert only 

would assume that minor assaults without mix of individual offenses, a substantial one-half a crime for each person crime in 

theft would involve fewer different offend- number of offenders must be removed the individual's rate of offending. i3ut this 

ers than rape, for example) nor the mix of from a population to affect substantially would be a reasonable estimate only if we individual and group offenses in an indi- the crime rate. also assumed that for group offenses the re- vidual's rate of offending, we cannot esti- Research on the effects on the crime rate of placement rate for incapacitated members 

mate with any precision what on the aver- incapacitating offenders generally makes a is 0 and that there are no deterrent effects 

age any offender contributes to crime simple presumption that each offense in an on the other group offenders as a incidents. We can say, however, that if an individual's rate of offending is a single consequence of incapacitating one of its 

offender were involved in a group incident, offender offense. Thus, it is assumed that members. 

it is not certain whether removing that the number of,crimes averted by incapaci- If we are reasonably correct in the fore- offender from that population of offenders tating an offender is equal to the individ- would have averted that incident. We can going argument, some more general inferual's rate of offending. Clearly that is not ences can be drawn. In investigating the also say that where offenders are largely generally the case when an individual com- effects of incapacitation on the crime rate, involved in group incidents, unless there is mits an offense as a member of an offend- it is assumed that incapacitation effects can a deterrent effect on co-offenders in the ing group. Were we to assume that ouresti- be separated from, and investigated apart event, it is unlikely that any crimes are mate of 2.1 offenders per crime against the from, deterrent effects. Clearly that is not averted by removing any single member of person holds for the person offenses in an the offender grow. We mav also infer that the case where group offending is involved. 

-. Whenever an individual is involved in unless offenses committed ky lone offenders are committed in substantial propor- group offenses, unless incapacitation of 

that member has a deterrent effect on the 

Percent distribution of incidents by size of offending group for selected types of crime incidents: 

All National Crime Survey incidents reporting offender information, 

July 1, 1972, to December 31, 1975 

Percent of incidents by size of offending group Total 


percent
 1 2 3 4 5 6-10 11-14 15-19 20t 


70.0 13.3 10.0 6.7 100.0 


79.5 11.6 4.5 1.8 1.8 0.9 100.1 


64.1 17.9 10.2 2.6 2.6 2.6 100.0 


81.9 5.7 3.8 2.9 1.6 3.5 0.6 100.0 


36.8 35.2 16.2 3.9 2.8 4.1 0.3 0.5 0.1 99.9 


44.8 23.7 15.3 6.0 4.2 5.4 0.3 0.2 0.2 100.1 


54.6 24.1 11.1 4.9 1.4 3.2 0.7 100.0 


49.7 22.8 12.7 5.6 3.4 4.1 0.9 0.4 0.5 100.1 


30.0 28.9 18.9 10.2 5.6 4.4 1 .O 0.5 0.5 100.0 


39.4 24.0 19.7 11.3 1.4 2.8 1.4 100.0 


59.7 12.6 9.1 6.1 3.1 5.8 1.4 0.7 1.5 100.0 


74.2 10.7 5.3 2.9 0.8 4.5 0.4 1.2 100.0 


44.3 23.5 18.8 b.6 1.6 5.4 0.4 0.4 100.0 


70.8 10.1 7.3 4.0 2.4 3.9 1.1 0.4 0.2 100.2 


67.2 12.4 7.6 4.1 2.7 4.2 0.7 0.4 0.8 100.1 . 70.6 11.0 6.7 4.0 2.6 3.9 0.5 0.3 0.4 100.0 


61.9 25.3 0.9 2.8 0.8 0.4 100.1 


61.4 24.3 8.9 3.5 1.5 0.5 100.1 


65.1 21.8 8.9 2.7 1.6 100.1 


52.6 30.5 10.5 4.2 2.1 99.9 


68.3 22.2 5.6 1.6 1.6 0.8 100.1 


61.4 25.0 11.4 0.2 100.0 


72.8 17.4 6.6 1.7 0.5 1 .O 100.0 


66.0 18.7 9.6 2.7 1.1 1.3 0.5 99.9 


60.0 25.0 9.2 2.5 0.8 1.7 0.8 100.0 


70.7 19.2 6.7 1.9 1.5 100.0 


66.7 19.0 5.7 4.7 2.1 1.4 0.4 100.0 


75.2 14.9 7.0 1 .O 1.7 0.3 100.1 


71.1 16.3 6.6 3.8 0.9 1.1 0.2 100.0 


73.3 16.4 6.4 2.0 1.1 0.7 0.1 100.0 


68.9 19.4 5.8 4.9 1 .O 100.0 


56.5 23.8 11.1 5.8 1.2 1.4 0.2 100.0 


71.6 17.6 6.8 4.1 100.1 


45.0 30.0 17.5 2.5 3.3 1.7 100.0 


78.6 7.1 7.1 7.1 99.9 


53.9 30.8 15.3 100.0 


14.210 3,505 1,932 925 51 7 749 120 61 88 


64.3 15.9 8.7 4.2 2.3 3.4 0.5 0.3 0.4 

- - 

other offenders involved with him, the 

effect of his incapacitation could easily be 

zero crimes averted, as the co-offenders 

could continue to account for the same 

number of crime incidents. if, however, the 

incapacitation of an offender has a deterrent effect on co-offenders, incapacitation 

may contribute substantially to reducing 

the crime rate. Any model of the effects of 

incapacitation on the crime rate should reflect deterrent effects on the network of 

offenders as well. 

Models of the effect of incapacitation on 

the crime rate assume that decreasing the 

prevalence rate of offenders in a population has a corresponding effect on the 

crime rate. There are several reasons why 

this may be a weak assumption. 

The models generally ignore replacement 

rates of incapacitated offenders. The size of 

an incapaciktion effect depends upon the 

size of the group, the fluidity of its boundaries, and the rate of replacement. To 

measure the rate of replacement is difficult, 

since much depends upon the age of the 

offender, the mix of offenses, the group 

contribution to an individual's rate of 

offending, the structure of social networks, 

and any other factors that affect changes in 

replacement rates. If we assume that individuals are inducted into criminal careers 

largely in co-offending and that offending 

networks are reasonably large, we would 

expect high replacement rates. Indeed, 

since within any offending group, or within 

a network of any reasonably large size, say 

ten or more, any individual offender is 

quite likely to be linked with different 

offenders in different offenses, it is possible 

that this condition of relatively free substitution of group members in committing 

any given group offense may work against 

replacement if any member is selectively 

withdrawn, i.e., the group is simply reduced in size. But it also is possible that 

ease of substitution in offending may generate recruitment and actually increase 

group size. 

Just how replacement takes place is qot 

well understood. It seems unlikely that any 

high offending group recruits directly from 

the nonoffending population and thereby 

increases the prevalence rate of offenders in 

a population. Rather, if one thinks of 

groups with fairly open boundaries in a The effect of incapacitation on replacelarger social network, then replacement ment rates is undoubtedly complex not 

follows somewhat the principles of replace- only for the reasons already mentioned but 

ment in a vacancy chain (White 1970). A because replacement occurs over a period 

vacated position in a high offending group of time. Replacement is not always an 

is more likely to be filled by marginal immediate response to vacancy. All other 

offenders than by new offenders. Recruit- things being equal, the longer a vacancy 

ment of new entrants to an offending popu- exists, the more likely any vacancy is to be 

lation thus is unlikely to occur by direct filled by processes of internal shifts into 

replacement in high offending groups but vacancies with a final closure by recruitindirectly in a chain of replacement; such ment from outside. Unless there are deterdirect effects on replacement will depend rent effects or substantial discontinuities in 

very much on the structure and extent of social networks that affect recruitment 

social networks. One might expect that net- levels, one would expect replacement to be 

works are more extensive and open in high fairly high. 

population density areas and areas where Nonetheless, one way that any organiza- crime rates are high. Thus one might expect tion may close off a vacancy is to vacate the higher replacement rates in large cities than position. Thus, it is possible that the effect in;ural areas. Similarly, replacement may 

be higher in young than older age groups 

since the boundaries of the former are more 

permeable and fluid. 

Table la: 

Type of crime -Not 

known 

Rape. w/theft 

Rape, no theft 1.8 

Att. rape, w/theft 

Att. rape, no theft 0.9 

Robbery, w/weapon 2.2 

Robbery, no weapon 4.6 

Att. robbery, w/weapon 1.4 

Att. robbery, no weapon 2.5 

Ser. assault, theft, weapon 4.2 

Ser. assault, theft, no weapon 12.3 

Ser. assault, weapon, no theft 4.6 

Ser. assault, no weapon, no theft 2.4 

Minor assault, theft 2.6 

Minor assault, no theft 1.3 

Att. assault. w/wea~on. no theft 5.2 

Att. assault; no weapon, no theft 2.4 

Purse snatch. no force 20.7 

Att. purse snatch, no force 3.3 

Pocket picking 56.5 

Burglary, forced entry, something taken 98.0 

Burglary, forced entry, 0 taken, damage 88.3 

Burglary, forced entry, 0 taken, 0 damage 86.8 

Burglary, unlawful entry, 0 force 93.4 

Buralarv. - .. att. forced entrv 91.6 - ..-

Larceny, $25O+ 95.7 

Larcenv. $1 00-249 96.7 

~arceny; $50-99 

Larcenv, $25-49 

Larceny, $1 0-24 

Larceny, under $10 

Larcenv, $ unknown 

Att. larcenv 

Car theft 

Att. car theft 

Theft, other vehicle 

An. theft, other vehicle 

Total number 

Percent 80.4 

0.0 = less than half of one percent 
of incapacitation on a group or network 

may be to reduce its size. But it is well to 

bear in mind that unless a group is at maxi- ' 

mum productivity, the same amount of 

work may be accomplished by a smaller 

number of members in a smaller number of 

positions. Reductions in prevalence of 

offenders in a population can always be 

offset by an increase in individual rates of 

offending. From a sociometric perspective, 

if the probability that any member of a 

group of a given size will be selected into a 

subset of offenders for a given offense is 

one in "n" incidents, then the elimination of 

any member may only increase his probability of being selected, which in turn intion may lead to quicker replacement than 

short-term incapacitation. 

We have noted that current models of the 

effect of incapacitation on the crime rate 

assume that reducing the prevalence of 

offenders in a population reduces the crime 

rate. We have proposed a more robust 

model, one where incapacitation can increase as well as decrease the crime rate. It 

also should be apparent that incapacitation 

can reduce the crime rate only under the 

conditions of less than total replacement in 

offending groups and no increase in the individual rates of offending of those who remain in the population. 

The proposed model assumes then that incapacitation can increase both the prevalence rate, through a complex process of 

recruitment to offending groups which 

actwlly increases the offending proportion 

of a population, and individual rates of 

oflending. Indeed, if the effect of incapacitating a member of an offending group increases the recruitment effort of all remaining members, the replacement rate might 

be greater than one, and the offending 

group might increase in size. Assuming 

that the supply of crime victims for a population of offenders is elastic, an increase in 

group size can increase the group offending 

rate. The ~roblem is undoubtedlv more 

creases somewhat his individual rate of complex since it depends upon both aggreoffending. It is also possible that replace- gate effects of recruitment in a population 

ment is related to the length of incapacita- of offenders and reallocation of offending 

tion of one of its members since the likeli- groups whose rates of aggregate offending 

hood ofereturn declines with the length of vary. 

expected absence. Long-term incapacita3 


Percent distribution of number of reported offenders by type of crime for all National Crime Survey incidents: 

July 1, 1972, to December 31,1975 

Number of offenders Offense Percent total reporting 

1 2 3 4 5 6-10 11-15 16-20 21+ Percent Number Offenden 

70.0 13.3 10.0 6.7 100.0 30 1 00.0 

78.1 11.4 4.4 1.7 1.7 0.9 - 100.0 114 98.2 

64.1 18.0 10.3 2.6 2.6 2.6 - 100.1 39 100.0 

81.2 5.6 3.8 2.8 1.6 3.5 0.6 100.0 31 9 99.1 

36.0 34.5 15.9 3.8 2.7 4.0 0.3 0.5 0.1 100.0 769 97.8 

42.7 22.6 14.6 5.8 4.0 5.1 0.3 0.2 0.2 100.1 625 9 5.4 

53.9 23.7 11.0 4.8 1.4 3.2 0.7 100.1 438 98.6 

48.4 22.2 12.3 5.5 3.3 4.0 0.8 0.3 0.5 100.1. . 599 97.5 

28.5 27.6 18.0 9.7 5.3 4.2 0.9 0.6 0.6 100.0 544 95.8 

34.6 21.0 17.3 9.9 1.2 2.5 - 1.2 100.0 81 87.7 

57.0 12.1 8.7 5.8 3.0 5.5 1.3 0.6 1.4 100.0 1,403 95.4 

72.4 10.4 5.2 2.8 0.8 4.4 0.4 1.2 100.0 250 97.6 

43.2 22.9 18.3 5.4 1.6 5.2 - 0.4 0.4 100.0 498 97.4. 

69.9 9.9 7.2 4.0 2.3 3.8 1.I 0.4 0.1 100.0 1,972 9g.7 

63.8 11.7 7.2 3.9 2.6 4.0 0.6 0.4 0.7 100.1 3,468 94.8 

68.9 10.7 6.5 3.9 2.6 3.8 0.5 0.3 0.4 100.0 6,087 97.6 

49.0 20.1 7.0 2.2 0.6 0.3 - 99.9 31 4 79.3 

59.3 23.4 8.6 3.5 1.4 0.5 - 100.0 209 96.7 

28.3 9.5 3.9 1.2 0.7 100.1 1 ,014 43.5 

1 .O 0.6 0.2 0.1 0.0 99.9 4,952 2.0 

8.0 2.6 0.7 0.2 0.2 0.1 1 00.1 1,077 11.7 

8.1 3.3 1.5 0.3 100.0 333 13.2 

4.7 1.1 0.4 0.1 0.0 0.1 0.0 99.8 9,073 6.6 

5.5 1.6 0.8 0.2 0.1 0.1 0.0 99.8 4,457 8.5 

2.6 1.1 0.4 0.1 0.0 0.1 0.0 1 00.0 2,796 4.3 

2.3 0.6 0.2 0.1 0.0 - 99.9 6,374 3.3 

2.3 0.7 0.2 0.2 0.1 0.1 0.0 1 00.1 8,057 3.5 

'2.3 0.5 0.2 0.0 0.1 0.0 - 100.0 9,700 3.1 

2.3 0.5 0.2 0.1 0.0 0.0 0.0 99.8 13,806 3.3 

2.4 0.6 0.2 0.1 0.0 0.0 0.0 99.9 22,368 3.4 

3.3 0.9 0.3 0.2 0.0 - 99.8 2,129 4.9 

10.2 4.3 2.0 1.0 0.2 0.3 0.0 99.8 4,667 18.2 

2.4 0.6 0.3 0.1 0.0 - 99.9 2,192 3.5 

4.0 2.7 1.6 0.2 0.3 0.2 - 99.8 1,344 9.2 

3.0 0.3 0.3 0.3 - 99.8 369 4.1 

11.3 6.5 3.2 100.0 124 21.O 

14,210 3,505 1,932 926 517 749 120 61 88 11 2,591 

12.6 3.1 1.7 0.8 0.5 0.7 0.1 0.1 0.1 100.1 19.6 
There is also a complex relationship between the mix of individual and group 

offenses in an individual's rates of offending and membership in offendinggroups. It 

does not seem reasonable to assume chat if 

an individual commits an offense at some 

times alone and other times as a member of 

an offending group that the lone offense is 

entirely independent of the group. There is 

some reason to believe that in the early 

stages of a person's criminal career, most of 

the offenses any offender commits are 

group offenses. Later criminal careers, by 

comparison, appear to have a larger proportion of individual offenses. Just how 

groups affect the propensity of persons to 

offend alone is not known. What is known 

is that among young offenders, the continuous lone offender is uncommon, but just 

how common he is at later ages is not 

known. 

Models for measuring the effect of incapacitation on the crime rate usually assume 

that individual rates of offendingare a constant-a tenuous assumption. Where variation is assumed, it is postulated that the 

distribution of individual rates of offending is such that a relatively small proportion of individualsmake a disproportionate 

contribution to the crime rate. If, however, 

individuals with high rates of offending 

account disproportionately for group offenses, then their contribution to the overall crime rate is substantially reduced. 

Correlatively, if high offending individuals 

are disproportionately lone offenders, or if 

offenses with a single offender contribute 

disproportionately to higher offender 

rates, then their contribution to the overall 

crime rate is substantially greater. The 

effect of selective incapacitation of offenders with high rates of offendingthen may be 

particularly sensitive to the mix of individual and group offenses in individual and 

group offending rates. 

Similarly, from the perspective of a group 

offending rate, if certain offenders are dis- . proportionately involved in most group 

offenses, their incapacitation may have a 

substantial effect on the group offending 

rate. This would be the case particularly if 

such high-rate offending persons are less 

easily replaced, and their incapacitation 

would have a greater deterrent effecton the 

propensity of less frequently involved offenders to commit crime than would the incapacitation of less frequently involved offenders on the propensity of the most 

involved offenders. 

It is conceivable that the selective incapacitation of offenders who are disproportionately involved in the offenses of a group 

might not have a substantial effect on the 

remaining members. Several conditions 

might offset the expected effect of incapacitation. One is that the remaining members 

recruit additional members (Hoekema 

1973). A second is that the group reallocates members of offending positions 

within the offending group. Short and 

Strodtbeck (1965) note that vacancies in 

the gang leadership position commonly are 

filled by reallocation. Another possible 

result is fragmentation of the original 

group and its members' selective recruitment to other groups where their individual 

offending rates might increase; or the remaining members might become two or 

more nuclei aro~ndwhich new offending 

groups form. In either case, there is a 

potential for increasing both the prevalence rate and individual rates of offending. 

Whether these alternative possibilities 

occur and with what frequency, or whether 

the deterrent effect on remaining members 

is the most likely result, requiresinvestigation. 

It is well to bear in mind that replacement is 

a continuous process in many different 

kinds of groups, including offending 

groups. The American population is fairly 

Table 2. 

Total 

Type of crime number 

offenders 

Rape, w/theft 48 

Rape, no theft 156 

Att. rape, w/theft 68 

Att. rape, no theft 513 

Robbery, w/weapon 1,780 

Robbery, no weapon 1,429 

Att. robbery, w/weapon 8 61 

Att. robbery, no weapon 1,382 

Ser. assault, theft, weapon 1,488 

Ser. assault, theft, no weapon 179 

Ser. assault, weapon, no theft 3,537 

Ser. assault, no weapon, no theft 480 

Minor assault, theft 1,164 

Minor assault, no theft 3,860 

Att. assault, w/weapon, no theft 6,996 

Att. assault, no weapon, no theft 11,676 

Purse snatch, no force 392 

Att. purse snatch, no force 327 

Pocket picking 679 

Burglary, forced entry, something taken 164 

Burglary, forced entry, 0 taken, damage 189 

Burglary, forced entry, 0 taken, 0 damage 68 

Burglary, unlawful entry, 0 force 876 

Burglary, att. forced entry 625 

Larceny, $250+ 2 12 

Larceny, 100-249 310 

Larceny, 50-99 474 

Larceny, 25-49 425 

Larceny, 10-24 705 

Larceny, under 10 1,095 

Larceny, $ unknown 157 

Att. larceny 1,530 

Car theft 114 

Att. car theft 238 

Theft, other vehicle 24 

Att. theft, other vehicle 42 

Total 44,263 

Percent, incidents against persons only 

Percent, all incidents 
mobile and transient. Turnover rates in the Codicil 	 References 

membership of schools and communities 	 Readers will be quick to detect weaknesses Hoekema, A. J. (1973) are very high where crime rates are high Rechtsnormen en Sociale Feiren: Theorie en 

and offenders are disproportionately con- in the proposed model for understanding 

changes in the crime rate and its implica- Empirie rond de Kleine Haven diefstal. Rottercentrated. This suggests that peer group dam. tien for conclusions about the effects of structures are far from static. There is con- deterrence and incapacitation on the crime Short, James F. and Fred L. Strodtbeck (1965) tinual recruitment and replacement of Group process andgang delinquency. Chicago: 

members. Just how substantial replace- 	 rate. Some will be quick to note that the 

structure of social networks and groups is University of Chicago Press. 

ment of members is for offending groups 

because of residential mobility is not 	 less formal than the argument supposes. White, Harrison (1970) 

Others will argue that human behavior is Chains of opportunity. Cambridge: Harvard 

known, but it is possible that transiency less rational than the argument assumes. University Press. 

itself has an effect on the prevalence rate of 

offenders in a population. The effects of 	 Still others will suggest that the burden of 

recruitment and replacement on offending evidence hardly warrants a model which 

may be greater for young than for older assumes human intervention to reduce 

persons and greater for closed than for crime rates may actually increase them. 

open social networks or groups. 	 And so it may be. Beneath the argument, 

however, lies a presumption that offending 

groups may not be all that different from 

other kinds of groups in a society. And the 

proposed model provides a basis for examining whether incapacitation may increase 

as well as decrease crime rates. 

J 

Percent distribution of estimated numJber of offenders by type of crime and mean number of offenders per incident 

for all National Crime Survey incidents where number of offenders was reported. 

July 1, 1972, to December 31, 1975 

Percent of offenders for each size of offending group 	 Number 

Total Number offenders of percent per 1 2 3 4 5 6-10 11-15 16-20 21+ incidents 

43.7 16.7 18.8 20.8 	 100.0 30 1.6 

57.1 16.7 9.6 5.1 6.4 5.1 	 100.0 112 1.4 

36.8 20.6 17.5 5.9 7.4 	 11.8 100.1 39 1.7 

50.5 7.0 7.0 7.0 4.9 	 18.3 5.3 100.0 31 6 1.6 

15.6 29.8 20.6 6.5 5.9 	 14.8 1.5 4.2 1.2 100.1 7 58 2.3 

18.7 19.7 19.1 10.1 8.7 	 19.0 1.9 1.3 1.5 100.0 603 2.4 

27.4 24.2 16.7 9.8 3.5 	 13.8 4.6 100.0 434 2.0 

21.0 19.2 16.1 9.6 7.2 	 14.8 4.9 2.7 4.6 100.1 59 1 2.3 

10.4 20.2 19.8 14.3 9.8 	 13.2 4.6 3.7 4.2 100.2 51 9 2.9 

15.7 19.0 23.5 17.9 2.8 9.5 	 11.7 100.1 7 1 2.3 

22.6 9.6 10.4 9.2 5.9 	 18.5 7.3 4.7 11.9 100.1 1,339 2.6 

37.7 10.8 8.1 5.8 2.1 	 19.6 2.7 13.1 99.9 244 2.0 

18.5 19.6 23.5 9.3 3.4 	 19.0 3.2 3.6 100.1 485 2.4 

35.7 10.2 11.0 8.1 6.0 	 16.7 7.4 3.3 1.6 100.0 1,958 2.0 

31.6 11.6 10.7 7.7 6.4 	 16.8 4.2 3.4 7.5 99.9 3,319 2.1 

35.9 11.2 10.2 8.1 6.7 	 16.8 3.6 3.0 4.5 100.0 5,991 1.9 

39.3 32.1 16.8 7.1 2.6 2.0 	 99.9 250 1.6 

37.9 30.0 16.5 8.6 4.6 2.4 	 1 00.0 202 1.6 

42.3 28.2 17.2 7.1 5.2 	 100.0 443 1.5 

30.5 35.4 18.3 9.8 6.1 	 100.1 95 1.7 

45.5 29.6 11.1 4.2 5.3 4.2 	 99.9 126 1.5 

39.7 32.4 22.1 5.9 	 100.1 45 1.5 

48.9 23.3 13.4 4.6 1.7 5.8 	 2.4 100.1 59 5 1.5 

39.5 22.4 17.3 6.4 3.2 6.9 4.3 	 100.0 379 1.6 

34.0 28.3 15.6 5.7 2.4 8.0 6.1 	 1 00.1 120 1.8 

47.4 25.8 13.5 5.2 8.1 	 100.0 21 0 1.5 

39.2 22.4 10.1 11.0 6.3 	 17.2 100.0 281 1.7 

53.4 21.2 14.8 2.8 5.9 1.9 3.8 100.0 303 1.4 

45.8 21.0 12.8 9.6 2.8 6.1 1.8 	 99.9 460 1.5 

50.1 22.5 13.1 5.5 3.7 3.9 1.2 	 100.0 753 1.5 

45.2 25.5 11.5 12.7 5.1 	 1 00.0 104 1.5 

31.1 26.1 18.2 12.8 3.3 6.7 1.8 	 1 00.0 851 1.8 

46.5 22.8 13.2 10.5 7.0 	 100.0 76 1.5 

22.7 30.3 26.5 5.1 8.4 7.1 	 100.1 124 1.9 

45.8 8.3 12.5 	 33.3 99.9 15 1.6 

33.3 38.1 28.6 	 100.0 26 1.6 

14,210 7.01 0 5,796 3,700 2,585 6,366 1,620 1,128 1,848 22,303 

30.2 14.2 12.7 8.5 6.3 16.1 4.1 3.0 4.9 100.0 	 2.1 

32.1 15.8 13.1 8.4 5.8 14.4 3.7 2.5 4.2 100.0 	 2.0 
Criminal opportunities and crime rates 


RICHARDF. SPARKS 

School of Criminal Justice 

Rutgers University 

A statistic very commonly used by criminologists is the crime rate-e.g., the 

number of crimes known to the police per 

100,000 population. In recent years, with 

the development of victimization surveying, similar use has been made of the victimization rate-e.g., the number of victimizations reported per 1,000 persons or 

households. It is argued here that such 

rates need very careful interpretation and 

that for many purposes they may be extremely misleading. It is also argued that in 

the calculation of such rates it is generally 

desirable to take into account opportunities for committing illegal acts as well as the 

population of potential offenders at risk. 

Purposes for which crime rates 

are calculated 

The purpose of this paper is to consider 

some conceptual and statistical properties 

of crime and/ or victimization rates. Before 

doing that, however, it is necessary to 

review briefly the reasons why such rates 

are used as measures of criminal behavior 

or its consequences and, more generally, 

why it has been thought important to 

measure crime or victimization in particular times or places. There appear to be four 

main reasons: 

1. Historically, the first purpose for col- letting statistics on crime and criminals 

appears to have been the measurement of 

the health,. of nations, cities, etc. 

The names given by the earliest demographers and statisticians to their measures 

of crime-Moralstatistik, statistique mo: 

rule-give a sufficient indication of this 

objective; if the numbers of crimes orcriminals increased, then in some sense the 

moral "health" of the nation was growing 

worse. Something of this concern appears 

to linger on In popular InterPretatlons of 

crime statistics: a rising crime rate is not 

infrequently seen as an indication of increased depravity or decreased probity, or 

as a sign of a usually ill-defined "social 

pathology." Somewhat similarly, Taylor, 

Walton, and Young (1975:42) have argued 

that from a radical perspective crime statistics can be used as an "examination of 

the extent of compliance in industrial 

society (in quite the same way . . . as it is 

possible to use statistics on strikes as an 

index of dissensus in direct class relations 

at the work-place)." 

2. A second purpose for measuring crime 

has been the evaluation of the effectiveness 

of the machinery of social control. As is 

well-known, Bentham (1778) was one of 

the first to urge that accurate measurement 

of crime was a necessary adjunct for the 

legislator; he urged the collection of statistics on convictions and prisoners as "a 

kind of political barometer, by which the 

effects of every legislative operation relative to the subject may be indicated and 

made palpable." 

3. A third reason for measuring crime is 

the estimation of the risk of becoming a 

victim. This concern is present, though 

often implicit, in contemporary efforts to 

develop "social indicatorsV(cf. Bauer 1964, 

esp. chap. 2). As victimization surveying 

has developed over the past decade, the 

assessment of risk has become increasingly 

prominent; indeed' it appears have been one of the main objectives of the National 

Crime Surveys (NCS) now being conducted 

by the Census Bureau for the Law Enforcement Assistance Administration (see Penick and Owens 1976:143-45). 

4. Finally, the measurement of crime has 

been a necessary preliminary to the devel- bpment and testing of criminological 

theories. Typically the testing of such 

theories has involved comparisons of crime 

rates in different places or types of place 

(for example, cities versus suburbs), or 

over time, or attempts at correlating 

changes in candidate independent or explanatory variables with changes in crime 

rates. 

It seems intuitively obvious that each of 

these four objectives requires the calculation of crime rates-that is, the number of 

crimes committed in a given place and time 

period must be standardized for the population in that place at that time period. It 

seems prima facie absurd to compare the 

number of homicides in the United Kingdom with the number of homicides in the 

United States, given that the United States 

has about four times as large a resident 

population as the United Kingdom; similarly, not much can be inferred from a comparison of the number of thefts in the 

United States in 1933 with the number of 

thefts in the United States in 1977, given 

that the U.S. resident population rose by 

over 70 percent in that time period. 

Whether our concern is with social morality, social control, the assessment of risk or 

the testing of theory, it is necessary to 

control for variations in crime which are 

due to differences in the numbers of persons able to commit crimes; criminological 

theories, for example, are theories about 

the causes of crime,-and not about population growth. Similarly, we would not conclude that people were becoming more 

dishonest, social control less effective, or 

life moredangerous, without standardizing 

for population size. 

The calculation of crime 

and victimization rates 

A simple rate, like a crime or victimization 

rate, is a function of only two elements: (I) 

a number of acts, events, situations, etc., 

which occur in a given place and time 

period; and (2) a number of persons or 

other elements present in the same place 
and time period. Thus a crime rate R is 

typically defined by 

where C = number of crimes committed, 

P = number of persons available 

to commit crimes, 

k = a number chosen either to 

give a convenient rate or a 

convenient base (e.g., 100,000 

persons). 

Thus a rate R.has a natural verbal translation: "For every k persons, R, crimes were 

committed." 

A victimization rate R, is typically defined 

in a similar fashion, but with two differences. First, the numerator of the righthand side contains the number of victimizations rather than the number of crimes; 

depending on the definitions of these two 

things, and the "counting rules" used for 

each, they need not be identical.' Second, 

the denominator is typically the number of 

persons, organizations, etc. capable of 

being viclirns. Thus the current NCS 

surveys, for example, compute commercial 

victimization rates to a base of (nongovernmental) recognizable businesses; no account is taken of the population of persons 

able to rob or burgle those businesses. (See, 

e.g., National Criminal Justice Information and Statistics Service 1976: 123.) 

Rates of this kind measure the incidenceof 

crime or victimization, since their numerators contain (essentially) numbers of 

events. But analogous rates can be 

constructed which measure the prevalence 

of crime-committing or being a victim; for 

such rates the numerator is usually the 

number of persons (organizations, etc.) 

who had committed one or more crimes, or 

been a victim on one or more occasions, in 

a given time period. Since a single offender 

may commit more than one offense in a 

given time period, or a person or organization may be a victim on more than one 

occasion, incidence and prevalence rates 

are not necessarily identical. (Compare 

death rates, where the number of deaths is 

necessarily identical with the number of 

persons who die.)2 

lForadiscussion ofthedefinitionsand "countingmies" 

used in the Unform Crime Reports, and their relation 

to those used in the National Crime Surveys, see 

Hindelang (197639-97). 

'In the case of phenomena which have some temporal 

duration (e.g., diseases), a further distinction is sometimes drawn between "point-prevalence" rates and 

"period-prevalence" rates. Crime and victimization 

prevalence ratesare of the latter type, i.e.. they give the 

percent of the population at risk who were criminals or 

victims within a time period such as a year. 

Crime and victimization rates raise a 

number of well-known problems of measurement. Typically we are interested in the 

numbers of crimes which are actually 

committed; but statistical series like the 

Uniform Crime Reports of course give only 

the numbers of crimes "known to the 

police." Similarly, victimization surveys 

aim to measure the numbers of victimizations which actually occur; what they get 

instead is the number of victimizations 

correctly recalled by survey respondents, 

reported to interviewers, etc. Each rate 

thus has, in its numerator, a "dark figure" 

of incidents which are not counted. Similar 

problems can also occur with the denominators of these rates, through underenumeration in a census; typically, however, 

these are much less serious. Having noted 

these problems of measurement, I shall 

from now on ignore them; my interest is in 

the interpretation of crime and/ or victimization rates, and not with the accuracy of 

the counts of incidents or persons which 

they may involve. 

The first of these problems of interpretation is a purely statistical one. It is obvious 

that a rate defined as in (I) is a kind of average; it is in fact a function of the arithmetic 

mean number of crimes committed per 

person. But such an average, taken over the 

whole of a population, clearly need not represent the experience of any individual or 

subgroup within that population. A death 

rate for the whole of a population-sometimes called a "crude" death rate-may 

conceal considerable variations in the incidence of death in various subgroups of 

that population. For this reason it is customary to calculate separate rates for subgroups whose experience is known to be 

different; e.g., age-specific or race-sexspecific rates, or rates associated with different causes of death as well as withdifferent populations. (Cf. Reiss 1967:22-23.) 

Such rates make possible between-group 

comparisons; for instance, of the risk of 

dying of heart disease at age 15 compared 

with the risk at age 75. Moreover, if the 

subgroups used to calculate such "specific" 

rates are reasonably homogeneous with respect to the phenomenon being measured, 

the resulting rates will not be very misleading as within-group descriptions of experience or risk. For example, if every white 

male aged 21 on his last birthday had an 

approximately equal chance of contracting 

smallpox by his 22nd birthday, an agespecific rate of infection of smallpox would 

give an accurate measure of risk to each 

individual, though of course it would not 

describe any individual's actual experience 

(since either he catches smallpox or hedoes 

not). The same thing is true for phenomena 

like crime or victimization, which can involve the same individual more than once 

in any noninfinitesimal time period. If 

every member of a given subgroup were to 

commit or suffer (say) exactly two crimes 

per year, then the resulting rate would 

necessarily reflect each individual's experiencce in that year. Though this is of course 

unlikely to happen, a crime rate would still 

not be too misleading, provided that the 

within-group variance were small, relative 

to the subgroup mean(i.e., in proportion as 

the coefficient of variation approached 

zero). Finally, even if the within-group 

variance were considerable, the rate might 

not be too misleading, provided the 

distribution were approximately normal 

(or more generally were symmetrical about 

its mean). 

It seems clear that this is generally not the 

case, however, either for crimes committed 

or victimizations experienced. Data from a 

number of studies to date strongly suggest 

that the frequency distributions of crimerelated events are typically extemely 

skewed, with the majority of the population 

having no crimes or victimizations in a 

given time period, and at the other extreme 

a small proportion of the population 

having a great many. It follows that a crime 

or victimization incidence rate will be an 

extremely misleading descriptor of the 

group's experience, or of the risk of crime 

or victimization. 

This point can be illustrated with data 

taken from a victimization survey which I 

conducted in three Inner London areas in 

1973 (see Sparks, Genn, and Dodd 1977, 

chap. 4). Table 1 gives the numbers of respondents reporting 0, 1,2, . . . incidents of 

victimization of various types as havinge 

happened within the survey reference 

period (approximately the calendar year 

1972), together with sample victimization 

rates per person. It will be seen that for two 

of the three areas, and for the sample as a 

whole, the total victimization rate is in 

excess of 1.0 per person. A naive interpretation of these rates might suggest that 
Table 1. Distribution of victimization incidents in three Inner London areas in 1972, and expected numbers based on Poisson I distribution (all three areas) 

I Number of 

incidents Brixton 

I Number Percent 

None 201 56 

1 40 22 

2 13 7 

3 14 8 

4 6 3 

5 2 1 

6+ 6 3 

I Totals 182 100 

Total numbers 


of incidents: 208 


Mean Numbers 


of incidents: 1.14 


everyone in the sample was a victim at least 

once in the year; or, alternatively, that the 

risk of victimization in those areas was 

about 100 percent, i.e., virtual certainty; 

yet, as the table shows, over half of the respondents in each area reported no 

incidents at all. 

Similar findings have emerged from a 

number of other victimization surveys 

done in recent years (see, e.g., Aromaa 

1971, 1974; Wolf and Hauge 1975; Reynolds 1973). The same general picture 

appears to be emerging from the NCS 

surve.ys. In the commercial victimization 

survey conducted in Houston, Texas, for 

example, the aggregate rate for robbery 

and burglary was 1.278 incidents per establishment; yet nearly 60 percent of the businesses surveyed reported no incidents at all 

as having occurred within the I-year reference period (see Penick and Owens 

1976: 127-30; Hindelang 1976:22). In the 

case of the NCS surveys this problem is 

especially serious, since in LEAA's published reports to date on these surveys, the 

victimization rate is virtually the only statistic used. 

Given a skewed distribution of the kind 

disclosed by Table 1, the victimization rate 

might still have some readily interpretable 

meaning in terms of victimization experience and/or risk, if the occurrence of multiple victimization were approximately 

random, i.e., if it more or less conformed to 

a Poisson distribution with the overall 

mean as a transition rate. As the right-hand 

column of Table 1 shows, however, this is 

not the case: the numbers reporting no victimization at all, and the numbers reporting several incidents, are both greater than 

would be predicted by a Poisson distribution. Compound distributions-based on 

Area I 

Hackney Kensington Total numbers i 

Number Percent Number percent 

1 04 58 93 51 

40 22 40 22 

11 6 32 17 

18 10 8 4 

2 1 3 2 

3 2 1 1 

1 1 7 4 

179 100 1 84 100 

151 223 

.84 1.21 

assumptions of "contagion" or increasing, 

probability of victimization (Coleman 

i964:299-305) or of heterogeneity of 

"proneness" to victimization (Greenwood 

and Yule 1920) give a somewhat better fit 

to data like those of Table 1; so does the 

skew distribution first described by Yule 

(1924) and discussed by Simon (1957: 145- 

64), which is based on slightly different 

assumptions. Using the London survey 

data an attempt was made to identify empirically (following a suggestion in Coleman 1964:378-80) subgroups of the sample 

with different mean rates of victimization, 

for whom the distributions of incidents 

could be adequately described by separate 

simple Poisson processes. Unfortunately, 

this attempt was unsuccessful. No set of 

criteria-based on attributes such as age, 

sex, race, or social class, either singly or in 

combination-was found by which the 

sample could be subdivided into groups in 

which the frequency distribution of multiple victimization was no greater than 

would be expected by chance. (See Sparks, 

Genn, and Dodd 1964: 166-67; for a similar 

analysis with no better result, see Aromaa 

1973.) 

In summary, in the present state of our 

knowledge, even specific subgroup rates 

are apt to be extremely misleading as descriptors of theexperience of, or the risk of, 

victimization. A prevalence measuresuch as the percentage who are victimized 

on one or more occasions in a given time 

period-is somewhat less misleading. But 

Number percent 

( A = 1.07) I 

298 55 187 

120 22 200 

56 10 107 

40 7 38 

11 2 10 

6 1 2 

14 3 1 

545 100 

582 -

- 1.07 

such a measure completely masks the extreme cases of multiple victimization which 

occur; if this is to be avoided, then the full 

frequency distribution must be presented.3 

Opportunities 

and rates 

The concept of opportunity is familiar in 

criminology, chiefly through the work of 

Merton (1938) and Cloward and Ohlin 

(1960).4 Though seldom explicitly referred 

to, the concept has also played a part in 

many less elaborate attempts to explain 

variations in crime rates over time or place. 

Thus, for example, it has often been noted 

that there are well-marked seasonal variations in observed patterns of crime, with 

crimes of violence typically being more 

common in the summer months and crimes 

such as burglary being more common in 

the winter: a common explanation for such 

findings is that social interaction is greater 

in the summer, thus providing greater 

opportunity for interpersonal violence, 

'Though the evidence is much less complete, it appears 

that the committing of crimes is distributed inasimilar 

fashion. Carr-Hill (1971) found that convictions for 

crimes of violence among adult males in England and 

Wales displayed a distribution not unlike that of Table I: 

most of the population had no convictions, while a 

small proportion had many. As with victimizat~on, a 

crime rate based on such a distribution would be extremely misleading: it would greatly overstate the involvement in crime of the majority, while, of course, 

understating the activity of the "crime-prone" 

minority. 

4Though it is interesting to note that, in general, both 

Merton and Cloward and Ohlin tended to regard legitimate and illegitimate opportunities as alternatives, 

and thus mutually exclusive: either one obtained a 

legitimate job or he joined the rackets. But-at least in 

Western industrial societies-the major opportunities 

for illegitimate gain open to most people involve theft 

of some kind from their places of employment: thus 

legitimate and illegitimate opportunity structures are 

intimately connected. For a study of blue-collar theft 

illustrating this point, see Horning (1964). 
whereas longer hours of darkness in the 

winter months provide greater opportunity 

for undetected entry into others' property. 

More recently, a few researchers have 

explicitly considered the relations between 

crime and opportunities for it. Before considering these approaches, however, we 

need to examine the relations between an 

opportunity for committing a crime, and 

the commission of crime itself. It is clear 

that, as a matter of ordinary language, the 

existence of an opportunity for a crime to 

be committed is a logically necessary condition of that crime's occurring. That is, if 

we are prepared to assert that an opportunity to commit, e.g., a theft at a particular 

time and place did not exist, then we should 

normally be compelled to say that no theft 

did in fact take place. Thus it is a necessary 

truth, and not merely a very well-confirmed 

hypothesis, that no motor cars were stolen 

in the United States (or anywhere else) in 

the year 1850; that no room air-conditioners 

were stolen in the year 1900; that no color 

television sets were stolen in 1930; and that 

no credit-card frauds were committed in 

1940. The opportunities for those crimes 

simply did not exist in those years. 

The proposition that changes in opportunities to commit crime will lead to changes in 

the numbers of crimes actually committed 

appears to be a hypothesis-to involve a 

contingent matter of fact, and not a truth of 

logic. But the matter is more complicated 

than that. Certainly it is not necessarily 

true that if the amount of stealable property increases, the number of thefts will, 

ceteris paribus, increase. However, a decrease in the quantum of stealable 

property, social interaction, etc., may of 

necessity lead to a decrease in thefts, 

assaults, etc., if it results in some individuals who formerly had opportunities to 

commit these acts no longer having them. 

Thus, suppose that in a time period 11 every 

member of a population of N persons has 

some opportunities to steal; a further increase in opportunities in that population 

may lead to more thefts, or it may not. Suppose at 12 the number of opportunities for 

theft is reduced, so that k individuals are 

completely without opportunities (so that 

thefts can only be committed .by N - k 

members of the population); all other 

things being equal, the number of the thefts 

will necessarily decrease. Evidently if we 

are comparing numbers of thefts committed at 11 and 12 we must take account of 

changes in opportunities between those 

two periods; and this is so whether tl precedes 12 or follows it. 

It follows that, for any of the four objectives 

of measurement mentioned earlier, opportunities for crime need to be taken into 

account in calculating crime rates for comparisons across time or place. Thus, if the 

crime rate is to be used as an indicator of 

social morality, probity, violence-proneness, collective wickedness, etc., it is in 

effect being interpreted as an average 

tendency in the population to behave in 

certain illegal ways; but a person's actually 

behaving in those ways presupposes that he 

has the opportunity to do so. Suppose that 

we associate with each person in the population a tendency to steal, assault others, 

etc.; borrowing a bit of economists'jargon, 

we might speak of a propensity to steal, 

assault, defraud, etc. Such a propensity can 

be defined as the conditional probability 

that an individual .will steal, assault, etc., 

given that he has the opportunity to do so. 

The evidence discussed earlier suggests that 

the distribution of this propensity in the 

population will be skewed rather than 

normal. The unconditional probability 

that an individual will steal, p(T), would 

then be given by the product of this conditional probability or propensity, and the 

probability p(0) that he has the necessary 

opportunity: 

But p(0) = 0 by definition, when no opportunities exist; thusp(T) will also necessarily be zero under those conditions. Thus 

if the average (or marginal) propensity to 

steal remains constant in a population between t~ and t:, but opportunities for thefts 

increase, the probability of theft (and 

probably the numbers of thefts actually 

committed) will increase; but that is not an 

indication that the population is becoming 

any more dishonest. In somewhat oldfashioned language, we might describe 

such a situation by saying that the number 

of temptations had increased (so that some 

who formerly had no such temptations 

available now had them); not that people 

were becoming any more susceptible to 

such temptations as they had. 

The unconditional probability p(T) can 

obviously serve as a transition rate in a 

Poisson process leading to actual thefts. 

The numbers of thefts occurring would in 

this case be a random variable depending in 

part on "theft-proneness" and in part on 

chance factors; models such as those of 

Greenwood and Yule (1920) would fit this 

situation. Such models assume that crimeproneness is not uniform in the population;, 

and while the evidence for this proposition' 

is admittedly thin, the proposition itself is 

intuitively reasonable. This point has been 

neglected in some recent attempts at modelling criminal behavior (see, for example, 

Avi-Itzhak and Shinnar 1973; Shinnar 

1975,1977). Shinnar does refer to the average number of crimes committed (which he 

designates by A) as a random variable; but 

since he deals constantly in theexpectation 

of this variable, he often seems to assume 

that it is literally the same for every member of the population of "criminals." This 

assumption may suffice for the purpose of 

making overall estimates of the hcapacitative effect of imprisonment: as Blumstein et 

al. (1978:69) have noted, most models of 

the incapacitative effect can be generalized 

to incorporate distributions of parameters 

such as A. (See also Greenberg 1975; Cohen 

1978.) But the assumption of a homogeneous A or proneness seems mistaken, if what 

is wanted is to model individuals'criminal 

careers (which is in fact important for some 

incapacitative strategies, e.g., those aimed 

at "high-risk" offenders). A further complication is that what may be called the "velocity" of individuals' criminal behavior 

probably varies; that is, A is probably not 

constant over time. For a discussion see 

Green (1978); and for a discussion of 

models which can be used to tackle such 

problems, see Fienberg (1977); Bartholomew (1973). 

The point being made here, however, is 

that p(T) is itself a function not merely of 

individuals' propensities to behave in certain ways (i.e., p(TI 0), which is the "real" 

proneness at issue), but also of their opportunities to exercise those propensities. The 

social and spatial distributions of those opportunities need to be taken into account, 

in any full attempt to describe or explain 

criminal behavior. 

A similar consideration applies if the crime 

rate is to be used as a measure of the system 

of social control, or as a dependent variable 

in a criminological theory or its testing. In 

each case, what the crime rate is supposed 

to measure is (approximately) the tendency 

of the population to behave in certain illegal ways, under specified control arrangements (e.g., a particular set of penalties) or 

specified social-structural or other conditions (e.g., a given level of unemployment, 

status integration, or relative deprivation). 

Plainly variations in opportunities must be 

controlled for, if changes in crime rates are 

to be interpreted correctly: a sharp decrease 

in opportunities for crime, for example, 

could be expected to lead to a decrease in 
Wilkins (1964:55). 

criminal behavior independently of any 

changes in presumed causal factors or the 

social-control system, merely because it 

was no longer possible for some people to 

commit crimes which they would otherwise 

have committed. 

Finally, variations in opportunity must be 

taken into account in assessing the risk of 

victimization. If, for example, the number 

of cars in use doubles while the number of 

ca,r thefts only goes up by fifty percent, then 

the average risk of a car's being stolen has 

declined; similarly, if people cease to go out 

of their houses at night, their risk of being 

assaulted in the street at night obviously 

declines. 

One of the first researchers to take into 

account variations in opportunity was 

Sarah Boggs, in her study of urban crime 

patterns (1965). Boggs noted that 

Environmental opportunities for crime vary 

from neighborhood to neighborhood. Depending on the activities pursued in different sections 

of the city, the availability of such targets as safes, cash registers, dispensing machine, 

people and their possessions varies in amount 

and kind. These differing environmental opportunities should be reflected in the occurrence rates [of crime]. (Boggs, 1965:899) 

Boggs noted correctly that a consequence 

of population-standardized crime rates 

was the production of "spuriously high" 

crime rates for central business districts, 

which contain relatively small resident 

populations but large amounts of merchandise, parked cars, and so on. Accordingly, she constructed "crime-specific" 

rates using denominators which could 

reflect opportunities for the type of crime 

in question: a business-residential land-use 

ratio for commercial burglary and robbery, 

the amount of street space available for 

parking, in the case of car theft, and so on. 

Rank correlations between these rates and 

rates standardized for population only, 

across 128 census tracts in St. Louis, were 

very high for highway robbery, residential 

burglary, rape, homicide, and aggravated 

assault; but they were low and in some 

cases negative for other offenses, e.g., T = 

-.23 in the case of nonresidential daytime 

burglary (Boggs 1965:901). 

It is important to note, however, that 

standardization for variations in opportunities for crime is not an alternative to 

standardization for the size of the population available to commit crimes (as Boggs's 

analysis suggests). Instead, both the population of potential offenders, and the stock 

of available opportunities for crime, 

should be reflected in the denominator of a 

crime rate. Thus, an opportunity-standardized rate R,* would be defined by 

where 0 = opportunities for the type of 

crime in question, 

k =a constant chosen to give a 

convenient base or rate (e.g., 

numbers of cars stolen per 1,000 

persons able to steal cars, per 

1,000 cars available to steal. 

(Note that R,* is defined as zero when 0is 

zero, since in that case Cis necessarily zero 

as well.) If we write RF1forthe opportunitystandardized crime rate in tl,and RF2for the 

similar rate in 12, then R? 1 < R*2if (C2CI)< 

(0201);that is, the rate will decrease if the 

number of crimes fails to increase as 

rapidly as the number of opportunities. It is 

also evident that if 02 = 01,then 

that is, if opportunities remain unchanged 

between 12 and 11,they can be ignored in the 

calculation of crime rates. This is also true, 

of course, for population. An opportunitystandardized crime rate thus uses in its 

denominator the elements of both crime 

rates and victimization rates, as these are 

usually calculated. 
The effects of taking into account opportunities can be illustrated by considering 

the data in Table 2, most of which are taken 

from Wilkins (196455). Column 2 of this 

table gives !he numbers of thefts from 

motor cars reported to the police in England and Wales during the years 1938-61 

(excluding 1939); column 3 gives the numbers of cars registered in England and 

Wales during those same years. Column 4 

contains the resident population of England and Wales in 1938-61 (General Register Office, 1964:Table 2). Column 5 is 

calculated from columns 2, 3, and 4, and 

represents the numbers of thefts per 

100,000 population per 1,000 cars available 

to steal; for convenience I have indexed this 

series so that 1938 = 100. The column 

headed "X" is also taken from Wilkins 

(196455); it is in fact the numbers of thefts 

from shops and stalls reported to the police 

in England and Wales in 1938-61. It is not 

clear to me why these figures were given by 

Wilkins, since he nowhere discusses them 

in the text of his book; they are, however, 

convenient for illustrative purposes. We 

may consider them to represent some candidate explanatory variable, e.g., average 

family income in pounds sterling. 

Wilkins's own discussion of the data in 

columns 2 and 3 of this table raises a 

number of questions. For one thing, he 

considers the numbers of thefts from motor 

cars, rather than the numbers of thefts of 

motor cars;s for another thing, he uses the 

numbers of thefts reported to the police, 

rather than the (reported) theft rate per 

100,000 persons, though as column 4 shows 

the resident population of England and 

Wales increased about 12 percent over the 

years 1938-61. inspection of the table will 

show that the numbers of thefts reported 

rose by about 350 percent, in the same 

years; the theft rate per 100,000 persons of 

course increased by somewhat less than 

this. The number of cars available to stealor to steal from-rose by over 200 percent, 

however; the result is that the number of 

thefts from cars, standardized both for 

population and for cars, rose by only 29 

percent. 

'Wilkins has since informed me that reliable data for 

thefts of cars were not available for the period in 

question. 

The effects of standardizing for opportunities can be quite striking. They may be 

quickly illustrated by comparing correlations between thefts from cars, and the 

same thefts standardized for both popuiation and cars available (i.e., columns 2 and 

5 of Table 2), and the (fictional) explanatory variable in the column headed "X". 

For the numbers of thefts and X, r = +.93; 

for the number of thefts standardized for 

population and cars registered, and X, r = -.21. Thus what at first sight seems a very 

strong positive correlation (+.93) is turned 

into a moderate negative correlation (-.21), 

when changes in the population and the 

stock of cars available are taken into 

consideration. 

The effects of population and opportunities 

may vary, of course, and may themselves 

be of interest. To illustrate the estimation 

of those effects, we may regress the numbers of thefts in Table 2 on population and 

the numbers of cars. It might be argued 

that the effects of population and opportunities were additive; intuitively, however, it seems more reasonable to assume 

that they are multiplicative, so that 

where T' = estimated number of thefts, 

C = the stock of cars, 

P = the population. 

This can be rewritten, after taking logarithms on both sides, as a 

which can be estimated using ordinary Least 

squares. A somewhat similar approach was 

recently used by Felson and Cohen (1977) 

in their analysis of burglary rates in the 

United States in the period 1950-72. Felson 

and Cohen utilize what they call a "routine 

activity" approach to crime, based on the 

human ecology theories of Amos Hawley 

(1950); they show that a substantial proportion of the variation in burglary rates 

can be accounted for (corrected R2 = .986) 

by a multiplicative combination of three 

variables, namely the percent of the population aged 15-24; the proportion of "primary individual" households; and an 

ingenious measure of the "inertia" of property targets, viz. the weight of the lightest 

television set advertised in current Sears & 

Roebuck catalogues. (See also Cohen and 

Felson 1978.) 

Similarly, using the data in Table 2, the 

numbers of thefts from cars can quite 

accurately be forecast from population and 

the numbers of cars registered (R2= .93). 

As 1 shaii argue later, however, it is often 

the case that neither the population at risk, 

nor the stock of opportunities, is of much 

theoretical interest; what is wanted, then, is 

to exclude their effects, and examine variations in crime that are "left over" after that 

exclusion. Thus, for example, after estimating the numbers of thefts from cars T', 

using equation (3a), we may calculate the 

residual thefts T* = T - T', and use those 

residuals as the dependent variable in subsequent analyses. (The correlation between 

those residuals, and the fictitious explanatory variable in column X of Table 2, is 

+.20.) It is to be noted that excluding the 

effects of population and opportunities in 

this way does not have the same effect as 

controlling for changes in opportunities (in 

this case, changes in the numbers of cars) 

by partial correlation. A partial correlation 

r,,., is of course a correlation between the 

residuals of the regression of x on z and 

those of the regression of y on z; the effect 

of the control variable z is thus removed 

from both x and y. In the present case, 

however, we are removing the effects of 

population and opportunities from the 

dependent variable only, in order to examine the residual variation in relation to 

some candidate independent variable or 

variables. (See, for a further discussion, 

Mosteller and Tukey 1977:269-71.) Some 

cases in which partial correlation and kindred techniques may be appropriate, in the 

analysis of criminal opportunities, will be 

discussed in a later section of this paper. 

In a more recent paper, Gould (1969) 

presented data similar to those given by 

Wilkins, for thefts of cars and numbers of 

cars registered, in the United States in the 

years 1933-65. Gould also compared yearend amounts of cash on hand in banks with 

the numbers of bank robberies and burglaries, during the years 1921-65. In each 

case Gould, like Wilkins, compared the 

numbers of thefts with his measures of 

opportunity, and took no account of 

changes in the population able to commit 

the two types of theft; in view of the fact 

that the U.S. resident population increased 

by about 50 percent between 1933 and 

1965, this is no small omission. (It might of 

course be appropriate to take into account 

'changes in the age structure of the population, or to exclude the effect of some subgroup thought to be especially likely to be 

involved in the partic;lar kind of crime in 

question-as Felson and Cohen (1977) did 
in their analysis of burglary.) Gould does 

not present, in his 1969 paper, data which 

would permit the calculation of doubly 

standardized rates of theft, or of residual 

theft after the exclusion of population and 

opportunity effects. But from his graphs of 

the two time series (Gould 1969:53) it is 

clear that both car theft and bank robbery/ 

burglary rates declined, relative to opportunities, up to about the middle 1940's; and 

that, even without allowing for increases in 

the population, rates relative to opportunities remained virtually unchanged from the 

mid-1940's to the mid-1960's. (The correlation between numbers of car thefts and cars 

registered is +.97, for the years 1950-65; for 

cash in banks and bank robberies/ burglaries, the correlation is +.98 for the period 

1944-65.) 

Still more recently, Mayhew et al. (1976) 

analyzed car thefts and numbers of cars 

registered, in London in the years 1961-74. 

They noted that the parallel trend noted . 	 earlier by Wilkins (for thefts from cars, and 

cars registered) did not continue, at least in 

London, after 1961. Mayhew et al. were 

mainly concerned with the effects of a preventive measure (steering column locks) in 

reducing opportunities for theft. Since 

1970, steering column locks have been required on all cars manufactured in or imported into England; the result has clearly 

been a decline since that date in the stock of 

what Mayhew et al. call "stealable" cars. 

Yet they found that the number of thefts 

of cars has continued to rise sharply in 

London, especially since 1970. If theft rates 

since that date were standardized for (declining) opportunities in terms of the 

numbers of unprotected cars, the increase 

in theft rates would be much greater than is 

suggested by the data which Mayhew et al. 

present. 

Defining and measuring 

opportunities for crime 

What constitutes an opportunity for the 

commission of a crime naturally depends 

on the type of crime in question, and satisfactory definition-both conceptual and 

operational-can in some cases be very difficult. One problem, to which I see no 

general solution, concerns the vagueness of 

the borderline between difficulty and impossibility, reflected by the Mayhew et al. 

(1976) study just discussed. Steering-column 

locks may deprive amateur car thieves of 

the opportunity to ply their trade; but they 

leave the opportunities open to professional car thieves (presumably) more or 

less unchanged. Similarly, the design of 

most bank vaults deprives the majority of 

the population of the opportunity to steal 

the valuables in those vaults; professional 

bank burglars, equipped with explosives or 

thermic lances, still have their opportunities available to them. In general, if preventive measures are themselves of theoretical 

interest-if, for example, it is intended to 

assess their effects on the crime rate-then 

those effects should be kept separate, and 

not excluded from crime rates in the way 

suggested in the preceding section. To the 

extent that one's interest is in other criminological factors, however, the opportunity-reducing effects of preventive or other 

social-control factors may best be removed 

from the crime rates in question, so the residual crime rates can be examined by 

themselves. 

There still remain many difficulties of definition. In the case of crimes of violence, 

opportunities are presumably created by 

contacts or interactions between persons. 

As is well-known, in a population of N persons, the maximum possible number of 

two-person contacts which can take place 

equals N(N - 1)/2; this was in fact the base 

used by Boggs (1965:900) in calculating her 

"crime-specific" rates of homicide and 

aggravated assault. However, this maximum number is of potential contacts of any 

kind (assuming-what is not off-hand 

clar-that the notion of a "contact"can be 

defined with reasonable precision). To be 

even approximately satisfactory, standardization for opportunities for crimes of 

violence would need to take into account 

the nature and duration (and possibly the 

frequency) of interactions between different types of persons, e.g., across different 

types of communities or in given interpersonal relationships. Thus some years ago 

Svalastoga (1962) analyzed a small sample 

of homicide cases in Denmark; he found, as 

have most-other researchers on homicide, 

that the majority involved family members 

and that strangers accounted for only 12 

percent of the cases studied. On the basis of 

a small survey of students, plus some admitted guesswork, Svalastoga estimated 

that a Danish person might have contacts 

with relatives, acquaintances, and strangers 

in the ratios 4. 10: 4. lo3: 4. lo6; on this 

basis, he calculated that the probability of 

being killed by an acquaintance was some 

3,000 times greater than the probability of 

being killed by a stranger and that the 

probability of being killed by a family 

member was some 600,000 times greater. 

These "probabilities" assume, of course, 

that the numbers and types of contacts are 

on average the same within each of these 

three groups, which is improbable to say 

the least. Nonetheless, the general logic of 

this approach seems to me correct; for the 

purpose of explaining the social, spatial, or 

temporal distribution of violent crime, as 

well as for assessing the risk of it, some 

account needs to be taken of the 

distribution of opportunities (i.e., interactions between persons) which are a 

logically necessary condition of such 

victimization. 

In the case of crimes against property, the 

choice of an adequate base for calculating 

an opportunity-standardized rate can also 

be problematic. One approach is simply to 

use the stock of stealable goods; this is in 

fact what was done by Wilkins, Gould, and 

Mayhew et al. in their studies of theft from, 

and of, cars. But for other types of theft, the 

matter is less clear. Thus Gould (1969), in 

analyzing bank robberies and burglaries, 

used data on amounts of cash and coin in 

banks. It might be argued, however, that 

the number of banking offies is a better 

measure of opportunity than the amounts 

of cash which are contained in those banking offices. (Data from the Statistical Abstract [US. Department of Commerce, 

19701 show that the amount of cash and 

coin in banks increased about five times in 

the period studied by Guuld; the number of 

banking offices increased by only about 70 

percent.) Similarly, should one use the 

number of supermarkets and/ or department stores as a base for shoplifting, or the 

value of those stores' inventories? The 

answer would seem to be that it depends on 

the purpose for which rates are being calculated. If the objective is the assessment of 

risk, then the number of institutions 

(stores, banks, etc.) would usually be more 

appropriate; if the objective is the explanation of observed patterns of theft, then the 

stocks of available goods might be 

preferred. 

In the case of thefts from individuals and/ or 

households, the choice of an appropriate 

base is even more complicated. In some 

places, estimates are available for the 

stocks of consumer goods owned by individuals and/ or unincorporated businesses 

(see, e.g., Roe 1971:70-71), where some 

estimated values for the United Kingdom 
in the years 1955-66 are given; these data 

are shown at written-down replacement 

cost, though if price-index changes are 

taken into account an estimate of physical 

stocks of goods coiild in principle be 

derived from them). In this country, data 

are available from the Statistical Abstract 

and from a variety of trade publications, 

such as Merchandising Week, on most 

types of durable consumergoods. Typically, 

these data are for ~roduction,shipments, 

or sales of such godds, though estimates of 

stocks can be derived from them if 

assumptions are made about average life 

(or average "stealable" life). Where figures 

for estimated stocks of such goods are 

available, they almost invariably disclose 

massive increases over the past three 

decades, usually far greater than the 

increases in burglaries and larcenies 

recorded in the Uniform Crime Reports. 

Thus, according to estimates based on 

market research by a television network 

(NBC 1975), only 9 percent of all American 

households had a television set in 1950; by 

1974 the figure was over 94 percent, with 

over two-thirds of those households having 

color television and about two-thirds 

having more than one set. (Similarly, trade 

sources estimate that the total number of 

radio sets in use in the United States 

increased by nearly 3% times in the period 

1950-74.) Within the past few years, there 

has evidently been an even more rapid 

increase in ownership of such things as 

stereo equipment, tape recorders and 

cassette players, hand-held calculators, and 

CB radios. The result has been to increase 

substantially the quantity of personal 

disposable property available to be stolen, 

and thus the opportunities for theft.6 In the 

case of television sets, for example, the 

figures just quoted mean that in 1950 a 

burglar or thief had less than one chance in 

ten of finding a television set in an American household chosen at random; by 1974 

he would have had difficulty in not finding 

6According to a recent newspaper account, moving 

companies estimate that the average household move 

involved 1,000cubic feet of goods 15 years ago; now the 

figure is about 2,000 feet. Not surprisingly, suburbanites are said to be "worse than city dwellers"in this respect. See "In age of accumulation, moving is a trial," 

New. York Times,March 19, 1978, p. R1. 

one, and in two houses out of every three 

could have had a choice of sets (or the 

chance of a color set) to steal. Over the 

same period-and for exactly the same, 

reason-the chance of any particular television set's being stolen has almost certainly decreased sharply. 

Until better data are available on the 

amounts and types of property stolen, it 

does not seem worthwhile to estimate 

changes in opportunities for theft with 

greater precision or detail. Unfortunately, 

little such information is now available. 

Since 1974, data have been collected 

(though not published) in supplementary 

returns from police forces under the Uniform Crime Reporting program; these 

returns, which have recently been made 

more detailed, apply only to thefts reported 

to the police, and nothing is now known 

about their validity. The same is true of the 

similar data now being collected in the 

National Crime Surveys. The Crime Incident forms (NCS-2 and NCS-4) used in 

these surveys contain questi~ns'~ertainin~ 

to the value (calculated in several different 

ways) of stolen or damaged property; but 

they are now coded so as to distinguish 

only between thefts of cash, motor vehicles 

and accessories, and "other" property. 

Given more data on the types and amounts 

of property stolen, it would, in principle, be 

possible to estimate the stocks of property 

from which those thefts occurred; if this 

were done, it would be possible to estimate 

rates of theft relative to opportunities, 

either cross-sectionally or over time. 

Opportunities and criminological' 

explanations 

Thus far, this paper has been concerned 

with the effects of variations in opportunities for crime-for example, changes in the 

stock of personal disposable property, in 

the case of theft-on the interpretation of 

the crime rate: it has been argued that, 

given the purposes for which we commonly 

measure crime, it is appropriate to standardize crime rates for opportunities. I can 

see no argument against this kind of standardization, which would not apply with 

equal force to standardization for changes 

in the population available to commit 

crimes. 

1969,1970; Mansfieid, Gould, and Namenwirth 1974) appear to treat changes in the 

stocks of one type of property-cars-in 

precisely this way. Thus Gould (196954) 

writes that "the availability of property influences the amount of theft against it," 

and he refers to this as a"causa1sequence." 

He goes on to speculate that "property 

crime is not only related to the availability 

of property, but ...this relationship is itself structured by the relative scarcity or 

abundance of the property being stolen." 

(Gould 196956)Healso notes that changes 

in patterns of car theft, and in the availability of stealable cars, parallel an apparent 

change in the population of car thieves, 

who (according to arrest data) are now 

much more likely to be juvenile or adolescent "joyriders" than they were in the 

1930's or 1940's. (Gould also notes that 

similar changes appear to have taken place 

among bank robbers, with "professional" 

robbers having largely been replaced by 

inept amateurs.) 

Gould suggests, then, that (at least so far as 

car theft is concerned) the period from the 

early 1930's to the early 1940's was "a 

period of economic scarcity" (Gould 

1969%) in which car theft was mainly an 

activity of "professional" thieves; and that 

the years after about 1942wereUmarkedby 

abundance," and the emergence of juvenile 

"nonprofessional" thieves. Inspection of 

the (graphed) data which Gould presents, 

however, suggests a rather different picture. From his graph of car registrations 

and car thefts, it appears that: 

Car registrations rose in the years 193341, 

though the increase would admittedly be 

less if increases in population were taken 

into account. 

Cars were possibly relatively scarce in 

the years 194145-there was a decline ,of 

about 16 percent, from about 35 million to 

about 30 million. 

Since 1945, the stock of cars registered 

rose steadily, but the numbers of car thefts 

fell, until about 1950. 

After 1950, the increase in car thefts 

roughly paralleled the increase in cars 

registered. 

It remains to be considered, in conclusion; 

whether opportunity factors also can or 

should figure as separate independent variables in an explanation of criminal behavior or variations in crime rates. Recent 

papers b.y Gould and his associates (Gould 
It is evident that none of these changes in 

stocks of stealable cars, and of car thefts, in 

any way necessitates the shift which 

appears to have taken place, from "professional" to "amateur" thieves; this change is 

quite independent. Moreover, the relation 

between cash and coin in banks, and numbers of bank robberies, is (as Gould 

[1969:56] puts it) "somewhat different"; to 

the extent that there has been a somewhat 

similar shift in the population of robbers, 

this is not paralleled by changes in the 

amounts of cash and coin available to steal. 

Using the concepts outlined earlier in this 

paper, we could in fact describe the situation relating to car theft in the following 

ways: 

In the years 193341, the numbers of cars registered rose fairly steadily, while the 

numbers of thefts of cars declined; the rate 

RT of car thefts standardized for opportunities fell sharply. Quite probably this 

could have been because, though it was 

successively easier to steal a car (there were 

more of them), it was also easier to obtain 

one legitimately. 

In the years 194145, when no new cars 

were manufactured and the stock of stealable cars declined, the numbers of thefts 

(and the theft rate R?) rose; because cars 

became relatively scarce, the opportunities 

for obtaining them legitimately also decreased. 

In the years 1945-50, the numbers of cars 

(and thus of opportunities for car theft) 

rose again; car thefts fell,so the car theft rate 

RT fell even more sharply; again this could 

have been because cars were more easy to 

obtain legitimately. 

Finally, in the years 1951-65, the numbers of cars (and of opportunities for car 

theft) rose steadily; so did the numbers of 

thefts, so that the car theft rate R? remained about unchanged. 

These temporal patterns areevidently compatible with many different combinations 

bf professional and amateur car thieves 

and different participation rates of each. 

In a later paper, Mansfield, Gould, and 

Namenwirth (1974) expand on Gould's 

earlier work (and incidentally standardize 

both car ownership and car theft for 

changes in population, as Gould had not). 

They attempt, using data from four countries, to test a model according to which 

thefts of cars (and, by implication, other 

stealable property) are determined by the 

interaction of "professional" and "amateur" 

demand for stolen vehicles, and the supply 

of available vehicles. The authors admit 

that they are only able to carry out a partial 

test of their model; in particular, they have 

no data on the relative magnitude of "professional" and "amateur" demand for 

stolen vehicles, nor on the shapes of the 

respective demand curves. Their paper illustrates two ways in which an opportunity 

factor-e.g., the supply of stealable goodsmay be incorporated into an explanatory 

theory. But it is important to note that it is 

not opportunities as such-in the sense 

described in this paper-that figure in such 

a theory. Instead, it is the relative scarcity 

or abundance of goods, which may affect 

participation in theft in, broadly speaking, 

one of two ways: (1) by affecting motivation to steal (e.g., by making it easier to 

obtain goods legitimately or conversely by 

increasing relative deprivation) and (2) by 

leading to changes in social control measures (in the broadest sense of that term, 

including measures for the protection of 

stealable property). Mansfield, Gould, and 

Namenwirth do mention both of these, but 

they make no attempt to operationalize or 

measure either one. The first of these explanations would seem to require (for 

example) some evidence about the dislribution of stealable property, as well as the 

quantity of it; it might also require consideration of the value of that property since 

(under certain conditions) an increase in 

supply relative to demand may lead to a 

decrease in price. Thus, for example, if 

more cars are available, opportunities for 

car theft will (ceteris paribus) increase; but 

it should also be easier to obtain cars legitimately. In this case we should expect a decrease in R?, such as that which occurred 

in the years 1933-41 and 1945-50. The 

second line of explanation might involve 

showing, for example, that when property 

is relatively abundant people are less likely 

to protect4t against theft, or to report thefts 

to the police. But an increase in the stock of 

goods-and thus in opportunities to 

acquire those goods legitimately-can 

occur together with an increase in protective measures; an example would be a law 

requiring steering-column locks to be fitted 

to all cars. (As Mayhew et al. [I9761 point 

out, such a law was passed in Germany in 

1963.) In this case the number of thefts 

would be expected to fall, for two distinct 

reasons: first because demand for stolen 

cars fell, and secondly because of a decrease in opportunities. 

One case in which it may be useful to treat 

changes in opportunities independently is 

the case in which they function as an intervening variable, helping to explain an 

observed relationship between crime or 

victimization and some other variable. 

Thus, several victimization surveys have 

found a negative association between age 

and victimization, especially for violent 

crimes such as assault (Sparks, Genn, and 

Dodd 1977:chap. 4; Aromaa 1971; Hindelang 1976:111-14). A possible explanation 

for this finding is that older people tend to 

go out less often, especially at night; they 

are thus less at risk of (certain sorts of) victimization. (What is opportunity from the 

offender's point of view, of course, is risk 

from the victim's.) If this factor is taken 

into account, the zero-order association 

between age and victimization may disappear, or at least be reduced. In our London victimization survey, for example, the 

zero-order y between age and victimization 

was -.42; between age and the number of 

nights per week the respondent went out, 

y = -.18; between nights out and victimization, y = +.20. The partial y between age 

and victimization, controlling for nights 

out, was reduced to -.29. A reasonable interpetation of these findings is that a part of 

the older respondents' lower victimization 

rate was due simply to the fact that they 

were less often at risk. A similar analysis is 

possible for some of the National Crime 

Survey data, since the NCS-6 "attitude" 

questionnaire administered to half of the 

respondents in the city-level surveys contains a question (Q.8a) asking "How often 

do you go out in the evening for entertainment?"; so far as I know, however, these 

data have not been analyzed from this 

point of view. 

Another case in which variations in opportunity need to be considered separately 

occurs when those variations are (hypothesized to be) consequences of protective or 

social-control measures in the broadest 

sense of that term. In the case of steeringcolumn locks on cars, for example, it 

would seem best to analyze thefts of cars 

with such locks separately from thefts of 

cars without them, taking into account the 

stocks of cars of each type; the hypothesis 

that locks were effective in preventing theft 

would predict that thefts of cars with locks 

would decrease (or increase less rapidly) 

relative to thefts of cars without them. In-
tensive (and highly visible) police patrols, 

anti-shoplifting devices, apartment-house 

security systems, burglar alarms, exactfare buses, and the like, may all beassumed 

to reduce some potential criminals' opportunities for crime, by making the successful 

accomplishment of crimes more difficult 

for the average person (or potential criminal). To the extent that our theoretical 

and/or practical interests are focussed on 

this kind of effect, we would not want to 

remove the effects of variations in opportunity from the dependent varilble (i.e., 

crime rates), but to treat them independently. If our interests lie elsewhere, however, we might well wish to remove those 

effects, so as to see better the effects of 

other variables on variations in crime. 

Inevitably, there will be borderline cases. 

The "inertia" measure used by Cohen and 

Felson (1977), discussed earlier, is an example. The fact that many durable consumer goods have become smaller and 

lighter (as measured by the weight of the 

lightest television set advertised in current 

Sears and Roebuck catalogues) can certainly be interpreted as increasing (the 

average man's) opportunities to steal. Are 

we interested in the effect of rhar change on 

rates of theft? Or are we interested in variations in theft of durable consumer goods, 

given that change in opportunities? Each of 

these questions requires a different measure 

of theft-the former excluding, the latter 

including, the effects of variation due to the 

opportunity variable. 

Suppose, furthermore, that the use of 

transistors, printed circuits, etc., has made 

some kinds of goods smaller and easier to 

steal (under average circumstances). Suppose, moreover, that (as is almost certainly 

true) those same technological factors have 

made those goods much cheaper (and thus 

generally easier to acquire legitimately). 

Suppose, furthermore, that-as is also certainly true-the stocks of such goods available to steal have increased sharply at the 

same time. In those circumstances, to treat 

prices, stocks, and "inertia" as separate 

variables in an explanation of theft rates 

will be likely to lead to severe problems of 

multicollinearity; but these will still be 

present, even if any one or two of the three 

(say, stocks of goods and "inertia") are removed, along with changes in the population, in the calculation of crime rates. 

Conclusions 

It seems that there are some instances in 

which variations in opportunities to commit crime may be substantively important 

in the explanation of variations in crime 

rates, and so should be treated independently rather than being "netted out" of the 

crime rates themselves. In general, however, it seems to me that variations in 

opportunities for crime are likely to be 

rather obvious and uninteresting where the 

explanation of crime is concerned. It is seldom useful to point out that cars could not 

be stolen before cars were invented; and it 

is not, in general, illuminating to point out 

that a man who never goes out of his house 

will never get assaulted or robbed in the 

street. 

But though they may often be relatively trivial in themselves, variations in opportunity 

may nonetheless often obscure the effects 

of more important theoretical variables. 

To avoid this, the procedure of standardizing crime rates for opportunities, as outlined in this paper, seems to me appropriate. This procedure is in fact analogous to 

the "method of residues" proposed some 

years ago b;y Coleman (1964: chap. 15). 

Coleman noted that a great deal of effort 

had at one time gone into finding a "law of 

social gravity" to the effect that, say, the 

amount of travel or other interaction 

between two cities is directly proportional 

to the product of their populations, and 

inversely proportional to some function of 

the distance between them. Such a "law" 

has the unfortunate defect that it often does 

not fit the observed data on intercity travel 

very well. But it also has the even more serious defect that, where it does fit, it is utterly 

uninteresting. By standardizing rates of 

travel for populations and distance, Coleman suggested, one could calculate for any 

pair of cities a "residue" which would be the 

difference between observed travel and 

that expected on the basis of population 

and distance alone; examination of these 

residues might then reveal more interesting 

effects which would otherwise be obscured. 

The same approach may often be useful in 

relation to crime and victimization. The 

number of homicides in New York is 

greater than the number of homicides in, 

say, New Orleans; but the homicide rare 

standardized for population is higher in 

New Orleans. The number of car thefts in 

the United States in 1965 is greatel than the 

number in 1945; but the car theft rare 

standardized for both population and the 

stock of stealable cars is smaller. Only by 

removing the sociologically trivial effects 

of population and opportunities can more 

interesting and important effects be seen. 

Many of the ideas in this paper were developed 

at the SSRC Workshop in 1975; earlier versions 

of the paper were presented at the annual meeting of the American Society of Criminology in 

November 1977, and at a Workshop on Quantitative Analysis of Crime and Criminal Justice, 

sponsored by the Institute for Social Research, 

University of Michigan, in August 1978. 1 am grateful to many people for their comments on those earlier versions: in particular to Don Gottfredson, Andrew von Hirsch, David Seidman, 

Howard Wainer, Colin Loftin, and Simon 

Singer. None of them is responsible for residual errors. 

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Notes on measurement 

by crime victimization 

surveys 

ALBERT D. BIDERMAN 

Bureau of Social Science Research 


Washington, D. C. * 


The first part of this paper describes shortcomings in victimization surveys in providing data for the measurement of the prevalence (rather than the incid.ence) of crime. 

The second part discusses the immunizing 

effects of victimization experiences to 

future experiences, and how the concept of 

immunization may be applied to the assessment of risk of victimization. 

The significance of measurements 

of events and conditions 

Incidents and conditions. Among many 

failures of the National Crime Survey 

(NCS) to derive the full potential of the 

victimization survey method that stem 

from the carryover into its conception and 

design of Uniform Crime Reports (UCR) 

rationales is its emphasis on crimes as 

incidents occurring at points in time. The 

survey method is more effective as a tool for 

gaining respondents' reports of their 

current states than of recalled events in 

even very recent and brief periods of their 

life histories. To a considerable degree, the 

significance of crime from a disaggregated, 

individual-oriented perspective (as opposed 

to a collective perspective) resides in 

durable consequences of victimization, 

rather than events of ephemeral consequences for the individual. While we must 

work toward developing elaborate procedures for stimulatipg recall in order to 

provide a survey instrument that will not 

grossly undercount even UCR Index 

crimes (conventionally labeled "serious"), 

we are, in the design of the NCS, neglecting 

almost totally gaining information on 

criminal victimization that is more readily 

approached as a condition than as an 

incident. We are also neglecting the 

durable consequences, that is, the changes 

in condition, produced by point-in-time 

incidents. In other words, NCS pursues an 

incidence, rather than prevalence, rationale. 

Among the kinds of victimization that may 

be conceived and measured in prevalence 

rather than in incidence terms are various 

forms of continuing terrorization and 

extortion, for example, the worker who is 

kept in line by union or company "goons," 

school children who must regularly yield 

their lunch money to fellow student toughs, 

the merchant subject to a shakedown 

racket, the prostitute terrorized by her 

pimp, or the spouse or sexual partner kept 

from separating from a hated relationship 

by fear of violence. 

To some degree, victimization surveys 

yield information about these kinds of situations through tabulations of what are 

called "series victimizations." In the NCS 

these are defined as three or more similar 

incidents of victimization mentioned by a 

respondent, but which, because of frequency and/or similarity, the respondent 

cannot individually date in time or differentiate descriptively from one another. 

(Were each incident of a series counted as 

one, they would form a very appreciable 

portion of all personal victimizations in the 

National Crime Survey; I would hazard a 

minimum of 20 percent of the total number 

of incidents.) Thus, the terrorized spouse 

may be identifiable in a victimization survey through repeated incidents of spouse 

beating, and the terrorized school child by 

repeated incidents of robbery. 

It is not necessary for a durable condition 

of victimization to exist, however, for there 

to be many incidents, each qualifying 

under the definition of a criminal victimization used by the survey. To make a threat 

credible to the victim and to continue a 

state of terrorization, the terrorist must 

neither continually repeat his threat nor 

demonstrate his willingness to carry it out 

by actually inflicting violence. 

Albert J. Reiss, Jr. (1972) also illustrates a 

somewhat different type of continuing victimization by the case of the tenant inhabiting a dwelling affected by building code 

violations. The "crime" of the landlord in 

this instance is similarly a state, rather than 

incident form of crime, that continues in 

duration through time, so long as the condition of the structure remains uncorrected. 

Bigamy has the same continuing character 

and involves a victimization where the bigamist keeps a partner ignorant of the other. 

Such victimization states are subject to incidence measurement with regard to points 

of entering or leaving the state, but prevalence measures are applicable to the observation of such victimization in a population. 

The series form of incident may also be an 

indicator of a condition of victim proneness, that is, a person vulnerable to offenses 

of a similar character by different offenders 

on frequent occasions. Among such conditions mentioned in victimization survey results are the shopkeeper in a high-crime 

area or the resident of a highly burglaryprone dwelling unit or the person who is 

forced to park his automobile where it is 

regularly subject to vandalization. 
While the NCS utilized the panel technique 

primarily to institute a control on "telescoping," the value of the panel feature 

probably will reside more in the elucidatiqi? 

of those forms of victimization best characterized in terms of prevalence, rather 

than incidence, measures. As indicated 

earlier, because inquiry can be made of current conditions of victimization, recall 

problems are avoided. Conditions are 

more accessible to survey detection than 

past events. In addition, their very duration 

or frequency in the individual life space 

makes the former more significant for individuals than are the many incidents with 

highly ephemeral consequences for individuals with which victimization surveys 

have been preoccupied. Finally, as Reiss 

has pointed out, such victimizations usually 

present a much higher potential for effective system intervention than is the case 

with point-in-time incidents. 

Another facet of victimization subject to a 

prevalence, rather than incidence measurement rationale, is the durable consequence 

of a point-in-time crime event. This is the 

rationale 1employed in my feasibility study 

of injury-produced handicaps and pain 

prevalence among A randomly sampled 

population. (Biderman 1975) 

Ideal control and compensation models. 

Elsewhere; I have discussed ideal models of 

society which can be posited by taking 

current ideas of crime control and victim 

compensation to their logical extremes. 

The "perfect" condition from which the 

victimization survey can be seen as measuring departures is one in which social life is 

so regulated that no one ever harms any 

other. To perfect a social order that is lessthan-perfect in this regard, a perfect compensation system can be posited; that is, 

one in which any victim of harm receives 

compensation (from the doer of harm or 

from the state) that makes him "whole" 

again. 

Our data problems can perhaps be understood in this way: we are able to construct 

intellectual models of social welfare that 

are much more integrated, comprehensive, 

and logical than are any institutions or 

social welfare we can actually bring into 

being. If we had (or could possibly have) 

the ideal welfare state with a perfect system 

of comprehensive social insurance, all 

harms befalling individuals would be recorded and measured as part of the process 

of social compensation (or state-enforced 

recompense by offenders). (Under these 

circumstances, indicators from the data of 

compensation would, of course, no longer 

be of individual concern, since the costs 

would be sccialized by perfect compensation. The social costs also would greatly 

exceed the aggregate value of individual 

harms because of the expense of operating 

the compensation system.) 

In current (as well as in conceivable) reality, 

we deal with limited systems of compensation. ~heoreticali~, victimization surveys 

would be needed primarily to measure the 

gaps, in scope and degree, between the 

actual occurrence of harms and the reach 

of the system of compensation. In actuality, however, the systems of social compensation are terribly poor at generating good, 

comprehensive statistics. In the United 

States, the factors of decentralization and 

the mixture of public and private systems 

make social and casualty insurance data 

close to useless for the purposes of social 

indicators of the "output" type. These defects of agency data place an additional 

burden on the victimization survey-that 

is, the survey is the only means currently 

available for gaining data on harms dealt 

with by systems of compensation, even 

though, with only modest perfections of 

the statistical operations of such institutions, such phenomena should be revealed 

with far greater scope and accuracy by data 

from transactions of the systems themselves. 

Two aspects of our earlier discussion bear 

on victimization surveys as a source of 

guidance for victim compensation systems. 

Data from the NCS havealready been used 

to estimate the costs of operatingcrirnevictim compensation systems. The orientation 

of casualty compensation, with an exception which will be discussed shortly, is entirely toward specific incidents of idss. To 

be administered economically, a crime 

compensation system would have to operate with a lower limit of liability, since by 

far the largest proportion of all incidents 

entail losses that are too minor to be worth 

the costs of processing them. The bulk of 

the data gathered by a victimization survey 

would fall below a reasonable threshold 

and therefore prove to be irrelevant to a 

feasible system of compensation. 

The discussion earlier showed that"trivia1" 

crimes can be significant, however. One 

significance they can have is when they are 

not isolated events but rather are associated 

with a status of the person making him vulnerable to continuing or repeated victimization. Public victim compensation systems, 

like private casualty insurance systems, are 

exclusively incident oriented and would be 

blind to such cases, .bowever. Compensation would also not deal with such costs to 

the victim as anxiety and the effects on 

behavior proceeding from anxiety. Private 

casualty insurance does have one form of 

interest in victim vulnerability, multiple 

victimization, and the hazards of local 

social environments-its interest in avoiding insuring anyone who might fall within a 

high risk class. 

A similar rationale applies to agencies for 

social control. The victimization survey 

should be necessary for data only with regard to instances of failures of (transgressions against) social controls which result 

in people being victimized by events that 

control systems aim to prevent, but which 

go totally unnoticed by these systems. In 

actuality, the survey is useful precisely because it helps compensate for the imperfections of control agencies as recorders and 

processors of information on their own 

transactions. 

Individualistic and reductionistic conlradictions. The recall problems of the victimization survey point to two contradictions 

in using the victimization survey for social 

indicators, where one seeks indicators 

which have the value standard of concrete 

harm to specific individuals. 

First, the relatively trivial and ephemeral 

consequences of most individual incidents 

of victimization which the surveys (and 

other offense statistics) seek to measure are 

precisely a major source of the recall difficulty that affects survey data and that 

makes expensive, brief-reference-period, 

large sample panel techniques necessary 

for their conduct. As was pointed out, were 

the survey oriented solely to victimizations 

having serious and lasting consequences to 

individuals, many of its methodological 

problems would be greatly alleviated. 

Surveys restricted in this way could beconducted far more economically and reliably 

than those which attempt to bring into 

their scope even just those incidents that 

qualify as "serious" by being in the set used 

by Uniform Crime Reports for a "Crime 

Index," or which are felonious or indictable under law. An early finding of the victimization survey method was that the bulk -
of such incidents entailed relatively minor misses most of the significance of most There is an explanation for an immunizing 

effects on the health or economic well- crime to the individual. effect of intersvecies victimization that is 

being of victims, relative, that is, to a host 

of other common hazards of daily life. 

They nonethe!ess were clearly seri~us from 

the standpoint of the offense given to legal, 

moral, and social norms. Aggregates of 

such incidents, furthermore, are of greater 

interest. For vulnerable individuals repeated victimization can be of major consequence as can be the fear of repeated 

victimization. The former-repeated victimization-directs attention, not to individual incidents, but rather to a pattern of 

vulnerability to victimization over spans of 

individual lives. While the latter-that is 

fears which may lead to costly alterations 

of people's life patterns-can result from a 

single and even minor incident of victimization, they arise when one's victimization 

is seen as related to a persisting condition 

of vulnerability specific to the individual or 

general to the community. For social indicators, particularly important are fears 

resting on perceptions of the extent to 

which norms and laws with regard to respect for persons and their property do or 

do not control the conduct of fellow inhabitants of one's community. 

One way in which we may seek to avoid 

criminal victimization is by individual 

action; that is, by being guarded in exposing one's property and one's person to 

others; by retreating, figuratively, into a 

constricted life behind defensible walls. To 

the extent that such guarded and constricted 

behavior becomes general and is successful, indexes of offenses and victimization 

would be kept down, but at vast costs in 

real freedom and in the richness of life. 

Another manner of protection is collective 

means; that is, through a normative system 

internalized by the processes of socialization and reinforced by both private and 

public sanctioning of deviance from the 

norms. It is upon these collective means, 

rather than individual guardedness, that 

we are mostly dependent for organized life 

in society. The role of crime counts as indicators of this social condition, of the vitality of the normative order, is what has 

elevated them as indexes to the major position as "social indicators" that they have 

always occupied since men first sought 

quantitative measures of the state of their 

society. Indicators of the extent to which 

people and organizations are guarded or 

trusting in their relations with each other, 

or feel they must be, would serve this purpose as well as offense or victimization data 

do. To look for the significance of crime 

exclusively in the concrete harm resulting 

from a given event to a specific individual 

There is a second contradiction in the individualistic, disaggregated orientation to 

victimization indicators which the vroblems of recall also bring to our attentibn. It 

is implicit in an assumption about motivation inherent in the survey approach. Cooperation with a public survey by a respondent makes little rational sense from 

the standpoint of individual self-interest 

for most respondents. For a few, participating in a lengthy interview on the subject 

of victimization may be a welcome intellectual and social diversion in lives otherwise 

barren of such experiences, but to most respondents, presumably, the survey constitutes an intrusion into a preferred round of 

activities. Cooperation with a survey does 

make rational sense, however, as a civic 

act; a citizen duty. If an interview is 

couched solely in terms of private significance, what should motivate respondents to 

recall and report in that interview events of 

relatively small private significance? Indeed, is it not a contradiction in itself to 

conduct surveys which depend upon a collective sense and a civic regard, and which 

are in themselves of value only in a collective way, yet have these surveys guided by a 

rationale to which nothing makes sense but 

private self-interest? 

Immunizing effect 

of exposure 

Early observations in victimization surveys 

found empirical distributions of the number of persons (Ni) victimized a given 

number of times (VI]in a time interval in 

which N,, was lower for all Vi > I than 

would be expected on the basis of a 

probability model that assumed an equal 

or random distribution of risk among the 

entire population and given the mean incidence for population. While refinements 

of the victimization survey method have 

produced distributions of n's of victimization having different shapes than this, and 

while there are many plausible post hoc 

interpretations in terms of both phenomena 

and method for the distributions of 

multiple victimizations that are observed, 

nonetheless, the problem invites consideration of a possible immunizing effect of 

victimization.1 

-

IWe are concerned here only with "natural immunization." 

captured in everyday speech by the phrase, 

"Once bitten, twice shy." There may be 

some virtue, however, in exploring the 

application of a medical analogy to criminal victimization. Considering such an 

analogy suggests some additional significant elements of immunization that are not 

suggested by the folk wisdom we have 

cited. Indeed, it is questionable whether 

avoidance behavior is a good analogy to 

the concept of immunization in medicine. 

Learning, or even unconscious avoidance, 

as a result of slight negative reinforcements 

does indeed produce less vulnerablility to 

more szvere perils from the same harmful 

agency or class of agencies as was the 

source of the original insult. For it to fit the 

medical analogy better, however, the victimizing experience has to result in some 

change in the subject that makes it less vulnerable to actual attacks by the criminal 

agent, rather than a behavioral change in 

the direction of avoiding that agent. Locks 

on doors, bars on windows, a burglar 

alarm system and other so-called "target 

hardening measures" as well as such steps 

as training in self-defense measures, carrying weapons on the part of individuals, and 

various adjustments on the part of merchants with regard to rearranging patterns 

of customer movement and merchandise 

display could all be illustrative here. 

Another form of immunization is the immunization from exDosures which controls 

overreactive respon'ses of a self-defensive 

sort. An analogy here can possibly be made 

to immunization from exposure to the 

effects of allergies. Experience with some 

forms of victimization: for example, petty 

theft or minor assaults, can develop the reaction, "It is not as bad as all that," and 

actual exposures to crimes of low consequence may eliminate relatively incapacitating adjustments such as extreme fear 

and behavioral circumspection. Residents 

and merchants in areas of fairly pervasive 

disorder may have such immunizing exposures against overreactive defense mechanisms. 

As in the case of medicine, however, both 

analysis and treatment in criminology confront the problem that a given exposure can lead to the mobilization of either appro-. 

priate or inappropriate defense reactions, 

depending upon complex relationships between the individual and his exposure to 

the agent. 

Thus far we have touched only on individuallevel immunization. Two kinds of social or 

collective perspectives can also be taken. 

The first is the development of a population immunity. This takes place when a sufficient number of individuals reach a sufficiently high level of immunity so that the 
survival of the offending species is affected. 

It takes place only when the offending 

agent is dependent for its survival on a 

population of hosts subject to immunization. It requires the creation of a very high 

level of long lasting immunity of a very 

large percentage of the population. This removes the opportunities for the criminal 

agent to survive and reproduce so that it 

approaches extinction. Levels of immunization in extent and efficacy below this 

level of population immunity can generate 

increased vulnerability. 

Population immunities also develop by the 

differential survival of its more immune 

members. This can occur with or without 

change in the prevalence of the-agent in the 

territory of the community or the mean 

virulence of the agent. An example of selective survival resulting in elevated population immunity would be decreased ecological burglary and robbery incidence rates 

occurring in a community as the most vulnerable small business establishments fail 

because of crime losses. There may be no 

associated decrease in the prevalence of 

offenders in the territory of that community (they may prey more outside its confines) and the offenders remaining may be 

more likely to use extreme measures in the 

offenses they do commit among the remaining "harder" targets. 

Another way in which the social analogy 

can be pursued is by regarding the community's defenses as the immunizing effects of 

exposure rather than individuals'. Most of 

the defensive adaptions to crime that are 

possible are collective ones taken at the 

community rather than the individual 

level. "Social defense" presumably requires 

prompt, effective immunizing reactions to 

low levels of attack. 

Most of the attention in criminology has 

been given to the effects of measures of 

social defense. "Victimology," however, 

concentrates its attention on the individual. 

Some recent evaluation studies, for example, in Portland, Oregon, have attempted 

to analyze the consequences of individial 

defensive measures for aggregate levels of 

crime incidence. Such studies logically 

present the statistical requirement for 

taking into account the effects of victimization subsequent individual and population vulnerability to victimization-a difficult and as yet untouched analytic problem. 

Risk of victimization 

Consideration of the concept of immunizing victimization may also help guard 

against tempting fallacies inherent in the 

frequent tendency to equate incidence rates 

with "risk." 

"Risk," first of all, conveys a future, rather 

than a past, temporal implication. If there 

is a high immunizing effect of exposure, the 

verv individuals who contribute to incideice during any period of observation 

may be precisely those who will be found to 

have been at low risk during some later 

period of observation (i.e., there will be few 

instances of repeated victimization). This 

may be the case even with no change, or 

even some increase, in the total rate for the 

community or class to which the victimized 

individuals belong, provided only that the 

supply of those vulnerable to victimization 

is very large relative to the actual incidence 

of victimization. 

Secondly, statistical risk inferred from an 

incidence rate for a population is expressed 

as a probability value for a member of that 

population. Distributions of individual 

risk, in the sense of future vulnerzbility, 

can be very unevenly distributed among the 

population, however. If the concept of risk 

is to be associated with an incidence rate, 

either there must be empirical and theoretical grounds for assuming a high degree of 

homogeneity of vulnerability among the 

population or care must be taken to use 

words that suggest the "risk" of aggregates, 

rather than individuals; 

This suggests additional difficulties with 

the risk concept. If there is a high concentration of victimization among some portion of a community, an inaccurately low 

measure of incidence for the entire community may more accurately reflect the risk 

rate for the large majority of the members 

of the population (or the median or modal 

"risk") than would an incidence rate based 

on a more exhaustive measure of incidence. 

There are good indications that this is 

indeed the case with rates based on victimization survey data in that small, but highly 

vulnerable, components of the population 

are most subject to underenumeration. For 

an aggregate risk level indicator most often 

most applicable by members of a community, that is, one descriptive of the "chances 

of my being victimized if the future resembles the past," an incidence rate that neglects the experience of both the most and 

least vulnerable components of the community would serve best. From the standpoint of social problem concerns, it may be 

only or mostly those who suffer frequent 

victimization and who benefit from no 

immunizing effects, who suffer appreciably 

at all. This is true where the effects of any 

one victimization are small, but repeated 

victimization may be costly or fatal. 

Determining which components of a community may be those most vulnerable presents very different statistical problems if a 

large proportion of all the victimization (in 

the real world or in that time slice of It that 

we can capture in our measurements) stems 

from many repeated victimizations of the 

same individuals than it is where repeated 

victimizations are rare or nonexistent (as in 

the case with homicide "risks"). The last 

case is analogous to the fatal or usually 

fatal disease. The only possible immunizing effect is one of population immunization by selective elimination of the more 

vulnerable. Rare multiple victimization 

can also be a function of extremely low 

levels of relatively randomly distributed incidence. High multiple victimization can be 

found associated with either very high but 

widely dispersed total incidence or with 

highly concentrated (ncnrandom) incidence. 

If multiples are rare, then we have no 

means for estimating a given individual's * 

vulnerablility other than by categorically 

associating him with some class that has an 

observed rate of incidence. (If multiples are 

rare because of fatality, we must use a statistical logic of nonreplacement.) If multiples are common, however, and if we are 

capable of making sufficiently long-term 

observations of individuals, then we can 

state empirical vulnerability rates for individuals and observe the stability of predictions of future victimization from observations of past victimization for each individual. If multiples are common because of 

concentration, this may yield only slight 

improvement over "risk" estimates based 

on-aggregate incidence for subclasses, providing the correlations of incidence with 

the ciassifications available are very high. 

If there is great dispersion, however, individual measures will be required for accuracy, as they will also be if there are immunizing effects of any great consequence. 

References 

Biderman, Albert D. (1975) 

"Victimology and victimization surveys." In 

1. Drapkin and E. Viano (eds.) Victimology: A new focus(vol. 111, Crimes, victims, and justice), 

Lexington, Mass.: Lexington Books. 

Reiss, Albert J., Jr. (1973) 

"Surveys of self-reported delicts." A paper 

presented for the Symposium on Studies of 

Public Experience, Knowledge, and Opinion of 

Crime and Justice, Washington, D.C., March 

17-18, 1972, revised July 1973. 
Victimization and the National Crime Survey: 

Problems of design and analysis 

STEPHENE. FIENBERG 

Department of Statistics 

and Department of Social Science 

Carnegie-Mellon University . 

1. Introduction 

Crime and its impact on society have long 

been the subject of public interest and social 

concern. While the study of crime has 

proved profitable to social scientists over 

the years, the limitations of police crime 

statistics (e.g., see Biderman and Reiss, 

1967) have always been viewed as being so 

great as to make it virtually impossible to 

measure criminality in a population. Hood 

and Sparks (1970) note that "Questions 

about criminality, like those about sexual 

behavior, are especially liable to distorted 

and untruthful answers." Thus it was with 

great anticipation that the social science 

community heralded the adoption of 

survey research methods to find the victims 

of crime, and to learn of their experiences. 

As a result of some small-scale attempts at 

victim surveys in the United States and 

Great Britain, and after considerable 

planning and preparation, the Law Enforcement Assistance Administration (LEAA) 

initiated a major new social statistics series 

based on a national victimization survey. 

The primary purpose of the national victimization survey, as stated in a planning 

document developed by LEAA, is "to 

measure the annual change in crime incidents for a limited set of major crimes and 

to characterize some of the socioeconomic 

aspects of both the reported events and 

their victims (Penick and Owens 1976, p. 

220)." Henceforth, we refer to this survey 

as the National Crime Survey (NCS), but 

the reader should bear in mind that the 

focus of the N CS is upon victims and their 

experiences with crime, not on crime itself. 

Actually the NCS consists* of four 

separate surveys: 

(1) A continuing national survey of 

household locations. 

(2) A continuing national survey of 

.commercial establishments. 

(3) A separate set of single or duplicated 

surveys of household locations in selected 

cities. 

'Since this paper was prepared, all but the continuing 

national survey of households has been discontinued. 

(4) A set of city commercial surveys to 

parallel (3). 


In this chapter we restrict our attention 


solely to the continuing national survey of 


household locations. 


The NCS has been designed and executed 

for LEAA by the U.S. Bureau of the 

Census and it includes personal interviews 

at six-month intervals with individuals in 

up to 65,000 households. Given the magnitude of the NCS and the massive files of 

data collected since the initial field work 

began in mid-July of 1972, it is remarkable 

that the NCS has received so little attention 

from professional statisticians outside of 

the Bureau of the Census. 

Central to an examination of victimization 

and the concepts underlying the NCS is the 

notion of a crime or criminal incident and 

how it gets recorded by various criminal 

justice agencies. The dictionary definition 

of crime offers little in the way of a starting 

point. For example, a recent edition of the 

Random House Dictionary defines crime 

as 

an action or an instance of negligence that is 

deemed injurious to the public welfare or morals or to the interests of the state nnd that is legally 

prohibited. 

To shed some light on this matter, Section 

2 describes in detail a single criminal incident, and notes how it would be recorded in 

statistics gathered by the police and in the 

NCS. 

Section 3 contains a brief summary of the 

survey and questionnaire design of the 

NCS, and describes some aspects of its execution. Special attention is focused on the 

panel structure of the survey design, with a 

rotation plan for households. The major 

shortcomings of the design are then noted. 

Sectipn 4 is brief and it summarizes the 

published analyses from the NCS. The lack 

of LEAA resources devoted to the statistical analyses of NCS data was one of the 

principal findings of the Panel for the 

Evaluation of Crime Surveys appointed by 

the Committee on National Statistics 

(Penick and Owens 1976, p. 3). This report 

contains considerably more detailed descriptions of the NCS survey and questionnaire design than we provide here. It 

describes the developmental research behind the design, and it suggests areas for 

further investigation. The conclusions of 

the report overlap considerably with ours 

regarding the need for extensive ongoing 

methodological research. 

Any assessment of the NCS must look 

closely at its objectives and determine to 

what extent they are being met. The primary purpose of the NCS as described 

actually has several components: 

(1) To measure the incidence of crime. 

(2) To measure the changes in crime 

rates over time. 

(3) To characterize socioeconomic aspects of criminal events and their victims. 

Closely related to item (3) are the aims 

(4) To identify high-risk subgroups in 

the population and to estimate the rate of 

multiple victimization. 

(5) To provide a measure of victim risk. 

From its inception, the NCS was viewed as 

a multipurpose survey that would produce 

not only the general-purpose victimization 

rates already described, but also data for 

policy-oriented problems; for example, 

(6) To calibrate the Uniform Crime Reports data produced by the FBI. 

(7) To index changes in reporting 

behavior. 

(8) To measure the effectiveness of new 

criminal justice programs (the city surveys 

were initiated for exactly this reason). 

To determine if the NCS properly fulfills 

aims (1)-(4) special attention needs to be 

Copyright @ 1978 by Academic Press, Inc. All rights of 

reproductionin any form reserved. ISBN:O-12-513350-2. 

Reprinted by permission, with minor changes, from 

Surve.rSoti1plinl: and Measurement (K.Namboodiri, ed.). 
focused on questions that utilize the longitudinal structure of the NCS. Section 5 

outlines a number of substantive questions 

regarding victimization and victim-survey 

methodology that in principle should be 

answerable by analysis of NCS data. A 

major stumbling block to the successful 

completion of these analyses is the highly 

complex NCS survey structure, designed to 

produce descriptive statistics rather than 

data -~ amenable ~ to analvtical studies of interrelationships and their changes over 

time. Although the NCS is a rotating panel 

in form, the primary purposes of the panel 

structure are to get more stable rate comparisons from one period to the next, and 

to bound the time frame under consideration. 

2. Recording crime 

Criminal incidents are events or social encounters involving one or more offenders 

and one or more victims, in one or more 

locations for specific periods of time. The 

duration of a single criminal incident may 

be 10 minutes, an hour, a day, a week, or 

even a month. Nonetheless, when put into a 

larger timeframe a criminal event is quite 

profitably viewed as the realization of a 

point process distributed over time and 

space, and we do so in Section 5. What 

complicates the modeling of a large number of crimes is the interpenetrating social 

networks linking offenders and victims, 

both within a single incident and across 

several incidents, and giving rise to multiple offending and multiple victimization. 

Reiss (1980). describes some of the impact 

of such networks and associated group 

structures on crime rates with special attention to the implications for measuring the 

effects of deterrence and incapacitation. 

The stochastic structure of criminal social 

networks and the resulting lack of independence of criminal incidents also has 

potentially important implications for 

both the design and analysis of victimization surveys. It is for this reason that we 

discuss some first steps in the stochastic 

model of victimizations for individuals 

over time in Section 5. 

How one records crime is a function of 

one's perspective. A single criminal incident 

or social encounter can involve one or 

more offenders, one or more victims or 

possibly no victims at all, and multiple violations of the law leading to multiple indictments of a single offender or several 

offenders who have participated in the 

event. There may even be mutual offending 

and victimization, for example, in cases of 

assault. Thus a particular configuration of 

crimes aggregated over a given time period 

may well look dramatically different when 

viewed from the perspective of offense 

rates as opposed to victimization rates, and 

neither set of ratesis likely to reveal the true 

nature of the criminal events that have 

taken place. 

A single hypothetical example can illustrate the comolexitv associated with crirninal incidents and tGe manner in which they 

are recorded. A.young couple living in the 

household of the woman's parents in Stamford, Connecticut, go to New York City on 

December 3 1 to celebrate New Year's Eve. 

They park their car in a lot on the east side 

of Manhattan and have a leisurely dinner 

at a nearby restaurant. After dinner when 

they return to their car, they are accosted 

by five young males just outside the parking lot and are taken into an adjacent alleyway, at approximately 11:OO p.m. One of 

the youths threatens the couple with a revolver, and the other four take turns raping 

the woman. When the woman resists, one 

of the youths assaults her with a knife, and 

then he also assaults the man. Following 

the acts of rape the youths take the 

woman's purse and the man's wallet, and 

they appear to flee. It is now about 1:00 

a.m., January I. The couple have to travel 

several blocks to report the incident to the 

police. When they finally return to the 

parking lot with a police officer at 3:00 

a.m., they discover that their automobile is 

missing. A week later three young males 

are stopped by the police in Newark, New 

Jersey, driving the couple's car through a 

red stoplight and they are arrested. 

The incident just described involved five 

offenders, two victims, three arrests, and 

numerous offenses including forcible rape, 

robbery, aggravated assault, and moior 

vehicle theft. It spanned several hours (and 

two calendar years!) and took place in at 

least two locations. How would it be classified by various recording systems? 

Let us begin with the police record of the 

event as it is transmitted to the FBI for use 

in its Uniform Crime Reports (UCR). In a 

multiple offense situation, the police classify each offense, and then locate the offense that is highest on the list of what is 

known as Part I Offenses (the ranking is 

criminal homicide, forcible rape, robbery, 

aggravated assault, burglary, larceny-theft, 

and motor vehicle theft). The highest 

offense is entered and the others are ignored. 

Multiple offenses need to be separated in 

time and place to lead to multiple entries in 

the UCR. The exeption to this rule involves 

crimes against the person (criminal homicide, forcible rape, and aggravated assault) 

where one offense is entered for each victim. Thus the UCR record will contain one 

offense of forcible rape (against the 

woman) and one offense of aggravated 

assault (against the man). Had the youths 

only robbed but not assaulted the man, there 

would only be one offense entered. These 

offenses would be recorded by the New 

York City police, and 1 am unclear as to 

which day (and thus which year) they will 

be attributed. The UCR record will also 

show that the offense(s) have been cleared 

(i.e., "resolved") by the arrest of the three 

youths in New Jersey. Although this event 

led to one or two UCR offenses, it might 

well lead to the prosecution of the five 

youths on up to a total of five counts of 

rape, 10 counts of aggravated assault and 

robbery, and five counts of motor vehicle 

theft. 

Suppose now that the couple's household is 

chosen as part of the NCS so that the event 

will also be recorded from the victim's perspective. Both the man and the woman 

would be interviewed separately and the 

NCS would record two victimizations in 

December: one for the woman "assaultive 

violence with theft-rape,"one for the man 

"assaultive violence with theft-serious 

assault with weapon." Even if the man had 

only been robbed but not assaulted there 

would still be two victimizations recorded 

(as compared with a single offense). Moreover, because of the separation of household victimizations from individual victimizations, when the woman's father 
reports the household victimizations, he 

may well report the theft of the car separately, and the month of victimization may 

be given as Janwry, and thus it could go 

into a separate calendar year. 

In summary, our single criminal incident 

involving five offenders and two victims, 

leads to one or two offenses recorded in 

New York and two or three victimizations 

recorded in Connecticut. The perspectives 

are clearly different, and so too are the 

records of the event. 

Because a large proportion of criminal incidents is never reported to the police, the 

discrepancy between all criminal offenses 

and those reported to the police has been 

described by Biderman and Reiss (1967) as 

the "dark figure" of crime, and one of the 

original purposes of victimization surveys 

was"to bring more of the dark figure to statistical light." Biderman and Reiss go on to 

note: 

In exploring the dark figure of crime, the primary question is not how much of it becomes 

revealed but rather what will be the selective 

properties of any particular innovation for its 

illumination. As in many other problems of 

scientific observation, the use ofapproaches and 

apparatuses with different properties of error 

has been a means of approaching truer approximations of phenomena that are difficult to 

measure. 

Any set of crime statistics, including those of the 

survey, involves some evaluative institutional 

processing of people's reports. Concepts, definitions, quantitative models, and theories must be 

adjusted to the fact that the data are not some 

objectively observable universe of "criminal 

acts," but rather those events defined, captured, 

and processed as such by some institutional 

mechanism [pp. 14-1 51. 

Much controversy has centered on the 

comparability of police statistics on offense 

rates and NCS survey statistics on victimization rates (e.g., see Biderman 1967; 

Biderman and Reiss 1966; Penick and 

Owens 1976, pp. 152-154; U.S. Department of Justice 1976b), but the utility (or 

lack thereof) of the NCS data for such comparisons should not obscure the richness of 

information about victimization available 

in the NCS. It is for this reason that the 

NCS data must be collected and organized 

in a manner that will make it amenable to 

standard forms of statistical analysis. 

Otherwise the rich veins of information on 

such topics as high-risk segments of the 

population and multiple vicfimization, or 

the way that deviance is perceived and dealt 

with in various social contexts, may never 

be mined. 

3. Design of the NCS 

a. Sample design 

The NCS is a sample survey of households 

and their occupants, and as such it closely 

resembles the Current Population Survey 

(CPS), which is also conducted by the 

Bureau of the Census, in almost all aspects. 

In fact, descriptions of the designation of 

housing units for the CPS (e.g., see 

Thompson and Shapiro 1973) are almost 

identical to those for the NCS (e.g., see 

U.S. Department of Justice 1976a,b), the 

major exceptions being the sample sizes, 

the interview schedules, and the panel and 

rotation group structures. 

The structure of the NCS is that of a stratified multistage cluster sample. The first 

stage consists of dividing the United States 

into approximately 2000 primary sampling 

units (PSUs) comprising counties or 

groups of contiguous counties. The PSUs 

are then separated into 376 strata and one 

PSU is selected from each stratum with 

probability proportional to population 

size. Within each PSU so selected, a systematically chosen group of enumeration 

districts is selected, and then clusters of 

approximately four housing units each are 

chosen within each enumeration district. 

For 1973, this process led to the designation of about 80,000 housing units, and interviews were obtained from occupants of 

about 65,000. Most of the remainingdesignated housing units were vacant or otherwise ineligible for inclusion in the NCS. 

The basic sample is divided in six subsamples or rotation groups of a little over 

10,000 households each. (Actually there 

are seven subsamples, but the data for the 

newest one are not incorporated into the 

reported rates. Rather these data are used 

for bounding purposes, as described in Section 3, a.) The occupants 12 years of age or 

older are interviewed at six-month intervals for a total of three years. Every six 

months a new rotation group enters the 

sample and the "oldest" existing rotation 

group from the previous sample is dropped. 

Each rotation group is divided into six 

panels, with one panel being interviewed in 

each month of the six-month period. 

For estimating various rates, a series of 

weights and adjustment procedures are 

applied to the raw data. The weighting procedures are standard practice for surveys of 

this sort and are basically designed to adjust for the differential probabilities of 

including various household locations in 

the survey, and to reduce bias and variance 

of sample estimators. The final adjustment 

involves the use of ratio estimation so that 

the distribution of individuals (or households) in the sample is in accord with independent estimates of the current population in each 72 age-sex-race categories. 

By reporting only adjusted rates, for both 

the NCS and the CPS, Census has removed 

from public scrutiny many of the actual 

defects of the sample design when it is 

actually implemented. Since all aggregate 

counts have essentially the same totals for 

various categories, we can never tell when a 

given sample is badly off the mark, nor in 

what directions. 

Although the NCS is basically a sample of 

household locations, at the same time it 

yields both a sample of households or families and a sample of individuals. Household 

locations are of little substantive interest in 

the study of victimization. While the NCS 

allows for the study of differential rates of 

victimization by type of household location 

(e.g., house, apartment, rooming house, 

mobile home), not one of the 100 tables in 

the LEAA report for 1973 (U.S. Department of Justice 1976b) deals with such 

information. The primary reason that the 

NCS is a sample of locations rather than 

households or individuals appears to be 

because Census has available a detailed 

frame only for locations. 

The NCS primarily measures victimization 

while the CPS primarily measures employment and unemployment. Since both unemployment and victimization are relatively 

rare phenomena, a naive person might 

suggest that a sample design that has 

proved successful for measuring unemployment should, with only minor modifications, do a good job of measuring 

victimization. Such a suggestion is naive 

because, among other things, it ignores the 

considemble knowledge we have available 

regarding crime and its physical as well as 

socioeconomic characteristics. In central 

cities, crime rates vary dramatically from 

block to block, and a limited amount of 

fieldwork might lead to cluster boundaries 

that differ dramatically from those that 
would seem appropriate for unemployment. 

It may well be that the NCS sampling plan 

is most sensible given budgetary constraints, 

but an exploration of alternatives and 

variants io the current plan should 

probably be included in the research, 

development, and evaluation program of 

the Bureau of the Census. 

b. Questionnaire design 

The questionnaire administered every six 

months at each household consists of two 

parts: a basic screen and crime incident 

reports. The basic screen includes household location information, household or 

family information, the personal characteristics of all of the individuals in the 

household (who may change from interview 

to interview), plus household or individual 

screen questions on crime. The report of 

the Panel for the Evaluation of Crime 

Surveys (Penick and Owens 1976) gives a 

detailed critique of the basic screen, and we 

refer the interested reader to their discussion. For each crime incident detected by 

the screen, a crime incident report 

containing answers to almost 100 questions 

is completed. 

The questionnaire distinguishes between 

individual identifiable incidents and series 

of at least three similar incidents which the 

respondent is unable to separate in time 

and place of occurrence. For individual 

victimizations, the questionnaire records 

the month in which the crime took place, 

but for series victimizations the respondent 

only needs to indicate the quarter(s) in 

which the incidents took place (i.e., spring, 

summer, fall, winter), the number of incidents (345-10, 1 I+, or don't know), and 

the details for the most recent event in the 

series. We discuss the distinction between 

single and series victimization in more detail in Section 4, where we note how the 

Bureau treats series victimizations and why 

we believe series victimizations should be 

the topic of extensive and analytical investigation. What is unclear to us from published documents and various unpublished 

memoranda is the extent to which series 

victimization is a true phenomenon or an 

artificial construct resulting from the NCS 

questionnaire design. 

Not only does the NCS questionnaire 

solicit information on the details of an 

incident, the offender, and any resulting 

physical injury and how it was treated, but 

it also inquires whether the incident was 

reported to the police and if not, why not. 

c. Reference period and bounding 	 ' no bounding for the new household or for 

One of the most crucial prbblems in the its members as individuals. Murphy and 

design of a victimization survey is eliciting Cowan (1976) report that unbounded 

accurate information on the time of households in returning rotation groups 

occurrence of criminal incidents. The comprise (for 1974-1975) 13.3 percent of 

problem has at least two components: the interviewed sample. In addition, only 

about 95 percent of the interviews in the (1) Recall decay. The longer the time bounded households are themselves bounded lapse between a criminal incident and the 	 due to considerable transience for house- date of interview, the greater the probabil- 	 holds in heavily urban areas. As a result, as ity that the event will not be reported to the few as 20 percent of the individuals over a interviewer. three-year period in a given set of house- (2) Telescoping. Events occurring in one hold locations may produce complete vic- time period can be reported as occurring in timization records for the period. These a different one. The displacement of tele- 	 design characteristics drastically impair the scoped events can be forward or backward utility of the NCS data for longitudinal in time. analysis of individual victimization profiles. 

It is especially difficult to model recall Considerable methodological interest is decay and telescoping, since such evidence 	 centered on the differences in victimization seems to point to differential rates ofdecay 

and telescoping for different types of 	 experience for migrants and nonmigrants. 

In addition to follow-up studies of out- crimes, and for different types of respondents. Moreover, there can be no check on 	 migrants (which are quite costly), it seems 

reasonable to do special analyses of the in- a crime that has never been reported, either 

to the police or the NCS. Thus the only way 	 migrants to the sample locations since their 

to get a handle on these two phenomena is 	 data are already in the NCS (see Penick 

via a sample of crimes reported to the 	 and Owens 1976; Reiss 1977b). For every 

police and the subsequent inclusion of vic- 	 out-migrant household there is an intims of these reported crimes in a victim 	 migrant one. Of course the current lack of 

survey. Such "reverse record checks" were 	 bounding for in-migrants would complipart of the pretests of the NCS survey in- cate such analyses, but it should be feasible 

strument (see U.S. Department of Justice to do a special study of in-migrants where a 

1972, 1974). The problem with drawing in- bounding period would be included along 

ferences from reverse record checks is that with additional interviews beyond the 

they are aimed at data which are missing 	 standard three-year period for the household location. from the victimization survev. but which 

are not missing at randome(see Rubin 

119761 for a discussion of the importance of 4. Published analyses 

the missing at random assumption). of the NCS data 

A consideration of both recall decay and Not only does the formal responsibility for 

telescoping is necessary for the determina- the design and execution of the NCS lie 

tion of the optimal reference period for a with the U.S. Bureau of the Census, but the 

victim survey. The NCS reference period is analysis of the collected data is also the re- six months, and Census uses the first in-. sponsibility of a small staff of Census em- terview and six-month period of ,a house- ployees. This analysis by LEAA and Cenhold location for bounding, that is, estab- sus involves the periodic preparation of 

lishing a time frame to avoid duplication of two- and three-dimensional cross-tabulaincidents in subsequent interviews. For a tions of estimated victimization rates and 

detailed study of theeffects of boundingon estimates of their standard errors. The 

telescoping, see Murphy and Cowan cross-tabulations produced are basically 

(1976). A major problem in the design of those requested in advance by professional 

the NCS arises because the bounding pro- staff at LEAA, and not as a result of a more cedures bound household locations, not detailed and complex statistical analysis. households or individuals. If one household replaces another during the course of Suppose for simplicity that NCS employed 

the three-year period during which a loca- a simple random sample and that the data 

tion is included in the NCS sample, there is (which are primarily categorical in nature) 

for any year were analyzed using some variant of loglinear model analysis for a kdimensional cross-classification (e.g., see 

Bishop et al. 1975). Then one of the implications of finding a model that gives a good 

fit to the data would be that the k-dimensional table may be succinctly summarized 
by a series of tables of smaller dimension, 

from which the original table can be reconstructed with essentially zero information 

loss. Such analyses can thus provide a 

rationale for reporting certain cross-tabw 

lations and not others. This point is described in more detail by Fienberg (1975). 

Even though the NCS does not employ 

simple random sampling, the idea of careful statistical analyses leading to the choice 

of cross-tabulations to be published is one 

which should be considered more seriously 

by LEAA and Census. 

How many reports has LEAA published 

on the results of the NCS national household sample? As of December 1976*, 

several preliminary but only two final 

reports had been released: a 162-page 

report on the 1973 survey (U.S. Department of Justice 1976b), and a much briefer 

73-page report comparing findings for 

1973 and 1974 (US. Department of Justice 

1976a). Since both final reports also 

contain data on separate commercial 

surveys, the interested reader is left with 

very slim pickings from what appeared to 

be a sumptuous meal. Moreover, these two 

reports contain only weighted data or 

proportions. No raw counts are available. 

Thus it is almost impossible for the skilled 

statistician to do extensive secondary 

analysis of the published data. 

When preliminary versions of the 1973 report were distributed by LEAA, several investigators noted that series victimizations 

were not included in the computation of 

any published rates or calculations. Thus 

all reported numbers and rates of victimization may be severe underestimates. For 

example, LEAA estimated for 1973 (U.S. 

Department of Justice 1976b) that there 

were approximately one million series victimizations in the personal sector and just 

over 20 million victimizations not in series. 

A series consists of three or more victimizations, and an average of five victimizations 

per series is likely an underestimate for the 

NCS data. (Some calculations based on an 

unpublished tabulation suggest that the 

average is in excess of six victimizations per 

series.) This then means that at least 20 percent of all victimizations in the personal 

sector have been excluded from the reported calculations. This matter becomes even more serious when we note that, in 

1973,46.3 percent of all personal series victimizations involved crimes of violence-

*The final draft of this paper was completed then. 

while only 26.6 percent of all victimizations 

not in series. Thus, series victimizations 

may have accounted for over one-third of 

all crimes of violence. 

We note that despite the panel structure of 

the survey, LEAA has yet to make use of 

the full longitudinal structure of the data 

base. The construction of a panel tape 

tracking individuals and households over 

time was not deemed to be a central goal of 

the NCS, and the preparation of such a 

tape was only belatedly arranged through a 

contract with a group at a private university. It might beargued that the panel structure of the NCS sample is intended to 

handle certain technical problems and to 

give more accurate year to year comparisons, and not for longitudinal analysis of 

individual files. Thiscan be true only in this 

narrowest of senses because without a detailed longitudinal analysis we can never 

know whether the aggregate annual reported victimization rates are at all accurate. For example, Reiss (1977), reporting 

on some preliminary longitudinal analyses, 

notes that highly victimized individuals are 

much more likely to be out-migrants than 

those with low victimization rates, and 

series victims are more likely to move than 

nonseries victims. Moreover, a high percentage of individuals reporting series victimizations in a given six-month period 

report no victimizations in the subsequent 

six-month period. These observations call 

into question the accuracy of the published 

victimization rates. 

5. Modelling victimization 

To understand reported annual victimization rates and the implications of changes 

in the'm from one year to the next, we need 

a detailed understanding of how victimization varies among individuals and subgroups within the population. This detailed 

understanding will necessarily have to 

come from the analysis of disaggregated 

data, and of individual victimization records over time. Such analyses will be complicated by the complex structure of the 

NCS sample design, but the effects of stratification and clustering on analyses will vary 

greatly from problem to problem. For 

many problems the use of unweighted data 

may well simplify the modelling process, 

This is clearly the case if we are interested in 

the structure of individual reported victimization patterns over time. 

The Panel for the Evaluation of Crime Surveys gives several suggestions for analytic 

research on the existing NCS data. One of 

these suggestions deals with the relationship between series victimization and multiple victimization, a topic we discussed in 

Section 4. To investigate this relationship, 

however, we need models for the occurrence of victimizations over time, and we 

propose one such model in siction 5b. A 

second suggestion deals with analyses to investigate under- and over-reporting of incidents as they relate to the month of incident 

and the month of interview. In Section 5a 

we take up some aspects that need to be 

considered in such analyses. 

a. Reporting biases and time-in-panel 

For several characteristics on which data 

are collected in the Current Population 

Survey, Bailar (1975) notes that there is a 

higher level for the first interview than for 

succeeding ones, and so on. The effect of 

such variation is usually referred to as "rotation group bias," and there is reason to 

expect such biases in the NCS data as well. 

In the NCS the rotation group bias problem is compounded by several factors including the elapsed time between the incident and the interview (recall that interviews provide data for the preceding sixmonth period). 

What we would like to do is develop a 

model which compares the victimization 

rates for specific crimes for a series of reference months as a function of the number of 

interviews, the time-lag from incident to interview, and other possibly relevant temporal variables. We build up to this in 

stages. 

In Table 1 we show the list of panels being 

interviewed by month of collection for a 

full three-year collection cycle, where the 

months have been labeled from 31 to 66. 

Panels 1-6 form a subsample that was first 

interviewed in months 1-6 (we ignore the 

initial interview for bounding purposes 

here) and leaves the sample after the interviews in months 31-36. Note that the difference between the month of collection 

and the number of a panel being interviewed equals the number of months the 

panel has been in the sample (time-inpanel). All three variables bear examination in terms of their effects on reported 

rates. The time-in-panel variable yields the 

rotation group bias information, while 
I month of collection measures seasonality 

and other unique temporal effects, and 

panel number represents temporal characteristics and effects unique to those that 

entered the sample at the same time.,The 

formal identity linking these three variables 

is the same as that linking age, period, and 

cohort as described by Fienberg and 

Mason (1978), and any model using all 

three as independent variables needs to 

take into account the identification problem associated with the linear components 

of the effects. 

Since each interview collects data for the 

preceding six-month period, for each refi 

erence month there are a total of 36 distinct 

panels which provide data. For example, 

panels l,7, 13, 19,25, and 3 1 provide data 

with a one-month lag for month 30 during 

collection month 31; panels 2,8,14,20,26, 

and 32 provide data with a two-month lag 

during collection month 32; and so on. 

Thus the ensemble of 36 victimization rates 

for a given reference month can be modeled 

as a function of month of collection, time 

lag to reference month, panel number, and 

time in panel (as well as various additional 

independent variables such as education 

and race if we wisb to compare subgroups 

of the sample). 

Of course we need to model several reference months simultaneously if we are to use 

all of the independent variables at once. If 

we in addition use reference month as an 

independent variable, then we have an 

additional identification problem related 

to the identity involving reference month, 

collection month, and time-lag until interview. 

To analyze and model data using the variables just described, we need to know 

whether we can treat the data for different 

reference months from the same panel as 

being independent. Moreover, it is unclear 

whether we should use rate as the response 

variate or counts of victimization (e.g., the 

number of respondents with 0, 1,2 .. . victimizations), and whether we should use 

weighted or unweighted data. 

Models of the sort we have just described 

need to be explored carefully if we are to 

get a proper handle on such problems as 

'rotation group bias and memory decay 

associated with recall. Modeline these 

phenomena separately (e.g., m ail& 1975; 

Finkner and Nisselson, Chapter 5, 1978) 

when they in fact occur simultaneously 

should only be the first step in an analysis, 

since it may lead to improper inferences 

unless there are order-of-magnitude differences in the sizes of their effects. What is 

Table 1. An illustration of the NCS panel rotation structure 

Panels being interviewed 

especially troublesome with any attemptto timization rate A, for crime type i, and that 

model these phenomena is that we candeal the expeded number of victimizations the 

only with individual victimizations, and individual will experience for crime type i 

not series, even though the latter may make in a fixed period of time T is simply A,T. 

up a sizeable proportion of the total This is, of course, the expected number if 

reported victimizations in a given period. we assume that victimizations follow a 

Poisson process. Since victimization is a b. A rnodelformultiplevictimizationsover rare event, in order to test the Poisson 

model we need to pool individuals into 

Most of the models that have been groups expected to have similar values of 

proposed for victimization assume that A,. Those victimization studies that have 

each individual has an "annual" vic- looked at victimization distributions for 

fixed periods of time and for subgroups of 

the population typically find that the Poisson model gives a poor fit. This may be an 

artifact of the data collection procedure, it 

may be a result of not using a fine enough 

disaggregation, or it may in fact be the 

result of the inappropriateness of the Poisson process. 
One more general structure for modeling 

victimization as a point process is the semiMarkov process, which includes the Poisson process as a special case. In this structure we view victimization as a point 

process ( Y(r), t >0}, where Y(t) =j if the 

individual were last a victim of crime type j. 

If the process is semi-Markov (see e.g., 

Cinlar 1975), then it has transition probabilities 

p,(t) = ~r{Y(t)= jl Y(0) = i}, (1) 

where i and j run over the possible types of 

crimes, say 1 < i, j < r. These transition 

probabilities can be expressed directly in 

terms of two sets of quantities: 

(1) A matrix of one-step transition 

probabilities governin a discrete-time 

Markov chain, M ={rn,$, which represent 

an individual's "victimization propensities" 

given his current victimization state. 

and depending on the last type of victimization. 

The transition probabilities are the unique 

solution of the system of equations 

where i,j= I, 2, . . . ,r, 

and J(t) is the probability density corresponding to the distribution function 

when the distributions F,(I) are kiponential, the process reduces to a timehomogeneous Markov one, and when, in 

addition, the probabilities {m, do not 

depend on i, that is, the rows are homogeneous, we get a set of Poisson 

processes. 

In order to use this general semi-Markov 

model for the NCS data, we need to see 

how the one-month-at-a-time data collection framework of the NCS can be embedded in the structure of the continuous 

time model. This problem resembles one explored by Singer and Spilerman (1974, 

1976a,b), who have used the semi-Markov 

process model of Eqs. (1) and (2) for investigating ~ccupationai mobility. In their 

work they have placed special emphasis on 

the embeddability of fragmentary multiwave panel data into a class of continuous 

time Markov models, and the identification problem within that class of models. 

The use of this class of models in the context of the NCS is complicated by the fact 

that as few as 20 percent of all individuals 

have full three-year records. Moreover, it is 

unclear whether we need to take into 

account the complexities of the sample 

design when we try to model the victimization histories of individuals with common 

sociodemographic and geographic characteristics. A final complication in the NCS 

data is the existence of series victimizations, which illustrate a strong propensity 

for rapid and repeated victimization of a 

specific type. Analyses based on underlying 

continuous time models certainly should 

include both series and separate individual 

victimizations. 

6. Discussion 

The two models described in the preceding 

section have not been explored with the 

NCS data, even in a preliminary form. 

They do, however, illustrate the problems 

involved in the analysis of data from the 

NCS when the purpose of the analysis is to 

provide estimates of aggregate victimization 

rates. While some have argued that modeling of this sort is unrelated to the primary 

objectives of the NCS, we disagree. First, 

we believe that an understanding of the 

basic structure of the panel data produced 

by the NCS is crucial to a proper evaluation of aggregate victimization rates. 

Second, the detailed stochastic modeling of 

individual records is required to directly 

meet one of the NCS objectives described 

in the introduction of this chapter: to identify high-risk subgroups and to estimate the 

rate of multiple victimization. Third, a 

reading of various documents about the 

NCS makes clear that it is in fact a multipurpose survey, and substantive issues and 

concerns need to be properly articulated so 

that the NCS design may be appropriately 

modified. 

Because the NCS is similar in sample 

design to many other large-scale social surveys such as the CPS, the Annual Housing 

Survey, and the National Assessment of 

Education Progress, it shares with these 

other surveys various methodological 

problems associated with data analysis and 

inference. For example, the weighting procedures used to get aggregate victimization 

rates and estimates of standard errors are 

not necessarily appropriate for other analytical purposes. To solve these problems, 

statisticians must develop variants of various multivariate techniques appropriate 

for the analysis of data from complex surveys. At the same time they must work 

toward the development of survey designs 

that are especially amenable to classes of 

analytical purposes, or at least to specific 

forms of analysis. 

Our evaluation of the NCS is well summarized by the following excerpt from the Report of the Panel for the Evaluation of 

Crime Surveys (Penick and Owens 1976): 

The panel has found much to commend, and 

much to criticize, in the design and execution of 

the NCS to date. We have argued that a very 

great amount of methodological and developmental research must be done, and many changes 

in existing procedures must be made, ifcertain of 

the specific initial objectives of the surveys are to 

be accomplished. The panel also maintains, 

however, that those objectives themselves need 

further scrutiny and that a subtle but fundamental change in the official concept of victimization surveying is necessary if the potential 

value of this relatively new research method is to 

be fully realized [p. 1521. 

This article grew out of material discussed in the 

Workshop on Criminal Justice Statistics held in 

Washington, D.C., July 1975, and sponsored by 

the Social Science Research Council Center for 

Coordination of Research on Social Indicators 

and the Law Enforcement Assistance Administration. The author is indebted to several of the 

participants of the Workshop whose ideas and 

suggestions inevitably have found their way into 

this article. In particular, thanks are due to 

Albert D. Biderman, Kinley Larntz, Albert J. 

Reiss Jr., David Seidman, and Richard Sparks. 
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crime incidence." The Annals of the American 

Academy of Political and Social Science 

374: 16-33. 

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"On exploring the 'dark figure' of crime." The 

Annals of the American Academy of Polirical 

and Social Science 374: 1-15. 

Bishop, Y. M. M., S. E. Fienberg, and P. W. 

Holland (1975) 

Discrete multivariate ana(tvsis: Theory and 

practice. Cambridge, Mass.: M.I.T. Press. 

Cinlar, E. (1975) 

Introduction to stochastic processes. Englewood Cliffs, N.J.: Prentice-Hall. 

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Social Indicators Research 2: 153-174. 

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"Identification and estimation of age-periodcohort models in the analysis of discrete archival 

data." In Sociological methodology 1979 (K. 

Schuessler, ed.), pp. 1-67. San Francisco: 

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Finkner, A., and H. Nisselson (1978) 

"Some statistical problems associated with 

cross-sectional surveys." In Survey sanlpling 

and measurement (K. Namboodiri, ed.), New 

York Academic Press. 

Hood,R., and R. Sparks (1970) 

Key issues in criminology. New York: 

McGraw-Hill. 

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National Crime Survey." American Statistical 

Association Proceedings ofrhe Social Sratirtics 

Section, part 11, pp. 633-638. 

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(1976) 

Surveying crime. Panel for the Evaluation of 

Crime Surveys. Washington, D.C.: National 

Academy of Science. 

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"Understanding changes in crime rates," this 

volume. 

Reiss, A. J. (1977) 

Personal communication. 

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6358 1-592. 

Singer, B., and S. Spilerman (1974) 

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populations." In Sociological Methodology 

1973-74 (H. Costner, ed.), pp. 356-401, San 

Francisco: Jossey-Bass. 

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Assistance Administration (1972) 

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Victim proneness in repeat viciimizaPion 


by type of crime* 

ALBERTJ. REISS,JR . Department of Sociology 

Yale University 

@ 

This paper explores whether victimization 

by crime is a random occurrence or 

whether some households and persons in a 

population are more vulnerableor prone to 

victimization and repeat victimization than 

are others. To do so: a crime-switch matrix 

is constructed for repeat victimizations and 

that distribution is compared with one 

expected under a simple assumption of 

random occurrence of repeat victimization 

by type of crime. Both households and 

their members are considered as units at 

risk. 

The paper also explores the error structure 

in a crime-switch matrix. The major types 

and sources of error are: 

(1) Errors in reporting month of occurrence of incidents and the absence of information on date of occurrence. 

(2) The absence of information on occurrence of series incidents so that their 

occurrence may be ordered in time and in 

relation to nonseries incidents. 

(3) Multiple reporting from members of 

a household. 

In examining observed switches in type of 

crime in repeat victimization, the following 

are noted: 

(1) Among repeat victims, given prior 

victimization by one of the most frequently 

occurring crimes (assault, personal larceny 

without contact, household larceny, and 

burglary) the most likely next victimization 

is by the same type of crime; for repeat victimization for the less frequently occurring 

crimes (motor vehicle theft, robbery, pursesnatching/pocket-picking, and rape), the 

most likely next victimization is the most 

frequently occurring of all major crimes, 

personal larceny without contact. 

(2) Nonetheless, there is substantial 

household proneness to victimization by 

the same type of crime. 

(3) Excluding proneness to repeat victimization by the same type of crime, any 

crime occurs about as frequently with any 

other type of crime over time as would be 

expected from the joint probability of their 

occurrence. Four symmetrical pairs of 

crimes occur less frequently than expected, 

however: assault with personal larceny, 

assault with household larceny, personal 

larceny with burglary, and personal larceny with household larceny. These are significant changers in a mover-stayer model. 

(4) The order of occurrence of a type of 

crime has no effect on the probability of 

occurrence of a pair. 

(5) The probability of consesutive victimization by the same type of crime varies 

directly with the probability of occurrence 

of that type of crime among all victims. 

The problem 

Considerable interest attaches to the 

question of whether victimization by crime 

is a random occurrence or whether some 

households and persons in a population are 

more vulnerable or prone to victimization 

and repeat victimization than are others. 

The question is not easily answered since 

theoretically one would want to model the 

distribution and behavior of both victims 

and offenders. Too little information is 

available at present to construct such a 

model. There is too little information on 

the distribution of offenders in a population and almost none on their networks or 

selection of victims. Do offenders, for 

example, select victims for their vulnerability to victimization? Similarly, while it is 

known that the risk of victimization varies 

considerably across territorial space, among 

different social aggregates, and over time, 

there is too little information on repeat victimization and the behavior proneness of 

victims. 

There are two major related and competing 

explanations for differences in the risk of 

victimization and repeat victimization: victim proneness and victim vulnerability. 

The victim proneness explanation selects 

personal, social, and behavior characteristics of persons as potential victims and 

their relationship to offenders as explanatory variables while the victim vulnerability explanation selects situations and characteristics of offenders, their networks, 

behavior and relationships to potential 

victims as explanatory variables. 

Simply put, victim proneness models 

explain high risk of victimization and repeat victimization by victim behavior and 

relationships with potential offenders that 

precipitates crimes or increases their vulnerability to potential offenders. The 

vulnerability models are more offender 

oriented, explaining repeat victimization in 

terms of such factors as the offender's prior 

relationship with victims, selection of criminal opportunities, and the organization of 

networks of offending. The considerable 

overlap of the models not only makes it difficult to test them as competing explanations but argues for a more general model. 

A more precise general model, however, 

depends upon yet to be acquired information on the behavior of both victims and 

offenders. 

*This paper is based on research supported by LEAA 

Grant #SS-99-6013. 
We can begin to answer our initial question 

of whether victimization by crime is a random occurrence or rather whether some 

persons or households in a population are 

more prone (or vulnerable) to victimization by crime by investigating the extent to 

which repeat victimization within the U.S. 

population conforms to a random model of 

occurrence. The National Crime Survey 

(NCS) makes it possible to examine repeat 

' victimization and the characteristics of 

repeat victims to determine whether certain 

kinds of victims are more at risk than 

others. This paper limits the examination 

to whether in repeat victimization of a 

household and its members, or of households only, there is a propensity to repeat 

victimization by the same type of crime. 

The answer to the question, by what type of 

crime is repeat victimization most likely to 

occur, given victimization by a prior type 

of crime, is obtained by constructing a 

crime-switch matrix for repeat victimizations and determining whether it conforms 

to anexpected model of occurrence under a 

simple assumption of random occurrence 

of repeat victimization by type of crime. 

The crime-switch matrix consists of pairs 

of victimization where a preceding victimization by type of crime is compared with a 

following victimization by type of crime. 

When the effect that victimization by a 

previous type of crime has on the occurrence of the next type of crime is examined 

in repeat victimization, the question arises 

whether the order in which the prior event 

occurs has an effect on the next reported 

type of crime. For example, in sequential 

or repeat victimization by a pair of any two 

types of crime such as personal larceny and 

robbery, is one as likely to be victimized by 

a personal larceny following a robbery as 

by a robbery following a personal larceny, 

given that the probability of occurrence of 

either a robbery or a personal larceny remains the same at both points in time? Or, 

is one more prone to robbery following a 

personal larceny than to a personallarceny 

following a robbery? We shall answer this 

question by investigating the degree of 

symmetry in paired victimizations by type 

of crime. 

Risk of victimization 

and victim proneness 

The question of what unit is at risk in victimization by any given type of crime or in 

repeat victimization by crime is not easily 

resolved. Among major types of crime 

measured in the NCS, a household is considered at risk for the offenses of burglary, 

household larceny, and auto theft while its 

individual members are considered at risk 

for offenses against the person, viz., rape, 

robbery, assault, larceny with contact 

(purse-snatching and pocket-picking), and 

personal larceny without contact. Yet, 

where each member of the household may 

purchase and own an automobile from individually earned income, an auto theft 

mav svmbolicallv represent more of a personal ihan a household crime. This m& be 

particularly the case where the household 

member is a young person who has purchased an automobile for his journey to 

work and personal use. Larceny of a paycheck from the principal wage-earner of a 

household, on the other hand, may symbolically represent a household rather than 

a personal Victimization. Similarly, an 

assault that incapacitates the principal 

wage-earner may be regarded as a family or 

a househgld victimization rather than a 

single member's victimization. 

Many, though not all, households consist 

of families who appear to regard any 

household crime as a victimization in 

which they share. On the averageanyadult 

member of the household can report more 

accurately the crimes against the household than the personal crimes against all 

members of the household. The NCS thus 

uses only a single member of the household 

to respond to the Household Screen Questionnaire to obtain information on crimes 

against the household while it asks each 

member the questions in the Individual 

Screen Questionnaire to obtain information on crimes against the person. Nevertheless, the NCS provides evidence that the 

household respondent does not always 

report all of the household crimes and 

additional household crimes, particularly 

burglary and motor vehicle theft, are reported by individual members in response 

to the Individual Screen Questionnaire or 

the Crime Incident Report (Dodge 1975). 

These matters of how information on personal and household crimes can most 

accurately be obtained aside, the evidence 

suggests that symbolically household members often experience a household crime as 

a personal as well as a household victimization. Where the household is a single-person 

household, a not uncommon condition, it seems unlikely that the member distinguishes the household collectively from his 

or her individual membership in it. Household and person crimes are probably experienced as personal victimizations in 

single-person households. 

Selection of the unit at risk in repeat victimization then is no simple matter. From 

one perspective the unit at risk is a household and its members; from another, it is its 

individual members. Yet in selecting either 

as the unit at risk, somewhat different 

assumptions are possible. Selecting the 

household as the unit at risk, one assumption is that it is at risk only for household 

and not person victimizations. An equally 

plausible assumption, however, is that the 

household as a collectivity is at risk so that 

household and person victimizations of its 

members are regarded as household victimizations. Selecting the person as the unit 

at risk, one assumption is that each member of the household experiences both 

household and person crimes as personvictimizations so that household victimizations should attach to each member of the 

household. An equally plausible assumption perhaps is that only the personvictimizations should attach to the person as the 

unit at risk. 

Each of these assumptions can be examined as the unit at risk for repeat victimization. Refinements in the unit at risk are also 

possible, such as by size of household 

(single-person, two-person, and three-ormore-person households) or for their composition in terms of families and unrelated 

individuals. The preliminary inquiry reported in this paper is limited to examining 

the household as the unit at risk. Crime 

switch matrices are constructed for the 

household as the unit at risk using all 

offenses against the household and its 

members (Tables 2-5) and for the household using only household crimes (Tables 

7-8). 

Construction of the crime-switch 

matrices and their error structure 

The crime-switch matrix is a cross-classification of pairs of crimes in the order of 

their occurrence in a sequence ofvictimizations over time. The number of pairs (p)in 

a sequence of two or more victimizations is 

one less than the number of victimizations 

(n), i.e., p = (n -1). There were 57,407 pairs 

of victimizations for households reporting 

sequences of two or more person and 

household victimizations and 16,884 pairs 

of victimizations for households reporting 

two or more household-only victimizations. 

All incidents fir households reporting two 

or more victimizations between July I, 

1972, and December 31, 1975, are included 

in our matrices. Since households and their 

members were in sample for varying 

lengths of time-from one to seven interviews-the probability of repeat victimization depends upon the length of time in 

sample. This fact is not taken into account 

in the construction of the matrices. Both 

bounded and unbounded incident data are 

included. 

Respondents initially define crime events 

in response to stimulus items in the Basic 

Screen Questionnaire. For each incident 

reported in the Basic Screen Questionnaire, 

a Crime Incident Report is completed that 

includes a large number of facts about the 

actual event. These facts are used to classify 

.events into particular types of crime victimization. Although there undoubtedly 

are some errors in respondent reporting, it 

is doubtful that they materially affect the 

classification by type of crime. When such 

errors occur, they should produce more 

error in detailed types than in major types 

of crime classifications. 

Reverse-record check studies show that 

errors occur in month of reporting the incident. These errors can have an impact on 

the ordering of events in time and thus 

affect the order of types of crimes in a pair 

in the crime-switch matrix. The procedure 

followed by the NCS, however, reduces the 

likelihood of these errors having a substantial effect since Crime Incident Reports are 

taken in the order of occurrence of events, 

beginning with the "first" incident. 

The Crime lncident Report of the NCS 

records only the month and not the date of 

reported occurrence of a nonseries victimization. For series incidents, the month in 

which the first incident in the series is reported as occurring is recorded; when that 

month lies outside the reference veriod for 

which crime incidents are beini recalled, 

the series is recorded as beginning in the 

sixth month of the reference period or that 

farthest from the time of interview. The 

seasons of the year during which the series 

incidents took place also are recorded. 

When more than one incident is reported 

taking place within the same month, they 

are not ordered by time of occurrence 

within the month. 

These survey questionnaire procedures 

make it difficult to order victimizations 

precisely. Where there is multiple victimization, crime incidents can only be ordered 

by month of occurrence and not within the 

month. Moreover, the incidents in a series 

victimization cannot be ordered by time of 

occurrence. Where both series and nonseries victimization are reported, series and 

nonseries incidents cannot be ordered by 

time of occuyrence. Given these survey 

limitations, a set of procedures was 

adopted for this report that orders victimizations in time.' These procedures are 

described below. 

First, using a random number generator, a 

date of occurrence was assigned to each 

nonseries incident within the month of the 

reference period for which it was reported. 

Where there was more than one incident 

reported within a given month, the assignment .of the date of occurrence was independent for each event. 

Second, a series incident was treated as 

only a single incident. The random number 

generator was used to assign a date of 

occurrence within the first reported month 

of occurrence of the series incident within 

the reference period. The type of crime 

assigned to the series incident was that 

reported for the most recent incident in the 

series since that is the only incident for 

which type of crime is reported. 

Third, merging all person and household 

series and nonseries incidents, the incidents 

were first ordered for each household and 

then reordered for household incidents 

only. The first ordering produced a household crime-switch matrix using all offenses 

against the household and its members and 

the second a household crime-switch 

matrix for offenses against the household 

only. 

'Other procedures may be adopted in later work. For 

example. for series incidents given the month of first 

reported occurrence of a series incident. the span of 

months (from seasonal data) for which they occur can 

be determined. Taking an estimate of the number of 

incidents in the series, we can then estimate an average 

time between series incidents. If we randomly assign 

dates of occurrence to these series incidents, they can 

then be merged with nonseries incidents. 

This procedure produces an unknown 

amount of error in ordering events within a 

month since the order of events within a 

month is determined from the randomly 

assigned dates of occurrence. 

Excluding all but one incident of a series 

also produces errors of two types. First, excluding series reduces the diagonal cells in a 

crime-switch matrix, i.e., the "stayers" in a 

mover-stayer model. A substantial proportion of all series victimizations would fall 

on the diagonal since on first reporting any 

victimizations, 76 .percent of all persons 

and 71 percent of all households report 

only series victimization within the 6-7 

month period. Not all cells of the diagonal 

would be affected equally since series victimization varies by type of crime. Second, 

in the remaining cases where both series 

and nonseries or two or more series victimizations are reported, there are misclassifications in preceding and following types of 

crime in order of occurrence. Such errors 

affect only the "changer" cells in a moverstayer model. On balance there is far more 

of the first type than of the second type of 

error since the number of events in a series 

is large relative to reporting of nonseries 

events within the same reference period 

and series only reporting predominates 

over series and nonseries reporting within 

the same reference period. Were all series 

to be included, then, one would expect even 

greater victim proneness (or stayer propensity) in our observed model. 

Table I presents the percent distribution by 

type of crime for all first and last reported 

crime incidents where the household and 

its members reported one or more crime 

incidents and the first and second incidents 

of a pair for all sequences of two or more 

victimizations. First and last reported 

crime incidents include the same crime 

incident when only a single victimization is 

reported but all ,first reported victimizations also include the,first reported incident 

in a sequence of victimizations and all last 

reported incidents include the last incident 

in a sequence. Where there are only two 

crime incidents in a sequence of victimizations, the first (preceding) and second (following) incidents may be of the same or different type of crime. In sequences of three 

or more victimizations, however, the 

second incident of a first pair becomes the 

first incident of the next pair in a crimeswitch matrix, and so on. Thus, all 

incidents in a sequence other than the last 

will appear as afirst incident in a pair and 

all but thefirst incident in a sequence will 

appear as the second incident in a pair. 
I 

-

Table 1. Percent of each type of crime by order of reporting victimizations of households and their members: AII household 

and person victimizations, July 1,1972, to December 31,1975 

Order of reporting victimization 

Reported as Reported as Reported as All reported Type of crime ~ ~ of a aair following ~ incident of a pair first incident ~ ~ preceding n incident r ~ e ~ 

Number Percent Number Percent Number Percent Number Percent Number Percent 

Rape 63 0.1 67 0.1 77 0.1 81 0.1 144 0.1 

Attempted rape 161 0.3 161 0.3 196 0.3 197 0.3 358 0.3 

Serious assault 959 1.7 932 1.7 1,346 2.3 1,316 2.3 2,279 2.0 

Minor assault 1,028 1.9 994 1.8 1,473 2.6 1,437 2.5 2,471 2.2 

Attempted assault 3,646 6.6 3,775 6.9 5,767 10.1 5,892 10.3 9,558 8.5 

Robbery 653 1.2 594 1.1 799 1.4 741 1.3 1,395 1.2 

Attempted robbery 429 0.8 384 0.7 649 1.1 606 1.1 1,037 0.9 

Purse snatch/pocket picking 752 1.4 715 1.3 610 1.1 573 1.0 1,328 1.2 

Attempted purse snatch 120 0.2 115 0.2 93 0.2 87 0.1 209 0.2 

Personal larceny, $50 and over 5,481 10.0 5,525 10.0 5,054 8.8 5,100 8.9 10,613 9.4 

Personal larceny, under $50 14.71 2 26.7 14,658 26.6 15,999 27.9 15,941 27.8 30,732 27.3 

Attempted personal larceny 1,428 2.6 1,483 2.7 1,463 2.6 1,517 2.6 2,954 2.6 

Burglary, forced entry 3,357 6.1 3,331 6.1 3,026 5.3 2,995 5.2 6,362 5.7 

Burglary, no force 4,646 8.4 4,689 8.5 4,375 7.6 4.41 7 7.7 9,074 8.1 

Attempted burglary 2,300 4.2 2,257 4.1 2,194 3.8 2,153 3.8 4,458 4.0 

Household larceny, $50 and over 3,350 6.1 3,307 6.0 3.31 1 5.8 3,269 5.7 6,621 5.9 

Household larcany,under $50 8,997 16.4 9,046 16.4 8,234 14.3 8,271 14.4 17,286 15.3 

Attempted household larceny 858 1.6 886 1.6 827 1.4 854 1.5 1,713 1.5 

Motor vehicle theft 1,331 2.4 1,403 2.6 1,151 2.0 1,223 2.1 2,562 2.3 

Attempted motor vehicle theft 730 1.3 704 1.3 763 1.3 737 1.3 1,469 1.3 

, Total 55,001 100.0 55,026 100.0 57,407 100.0 57,407 100.0 11 2,623 100.0 

*The entries for "Reported as first incident" and "Reported as following incident of a pair" do not always sum to the Total, "All 

reported incidents." for each tvpe of crime; there are 21 5 incidents for which month of occurrence is unreDorted. 

Table 2a. 

Type of crime 

"reported as 

preceding incident Rape 

Att. 

rape 

Serious 

assault 

Minor 

assault 

Att. 

assault 

Att. 

robbery 

Purse 

snatch, 

pocket 

picking 

Rape 6 3 8 1 5 2 2 1 

Attempted rape 1 16 6 9 21 1 6 2 

Serious assault 2 11 119 75 21 2 37 19 18 

Minor assault 4 8 83 152 244 22 20 21 

Attempted assault 11 29 199 228 1,685 59 81 37 

Robbery 

Attempted robbery 

2 

1 

4 

5 

50 

30 

30 

21 

76 

72 

89 

27 

27 

54 

23 

12 

Purse snatchlpocket picking 

Attempted purse snatch 

1 2 21 

3 

19 

2 

47 

10 

26 

2 

9 

3 

46 

1 

Personal larceny, $SO+ 

Personal larceny, under $50 

7 

16 

15 

33 

110 

238 

99 

292 

401 

1,314 

61 

1 26 

44 

136 

44 

144 

Attempted personal larceny 

Burglary, forced entry 

Burglary, no forcible entry 

Attempted burglary 

Household larceny, $50+ 

Household larceny, under $50 

1 

7 

9 

4 

7 

3 

17 

11 

8 

8 

18 

25 

90 

85 

46 

62 

89 

34 

59 

107 

46 

61 

154 

11 5 

199 

31 9 

166 

238 

554 

22 

42 

45 

30 

43 

75 

24 

25 

34 

15 

24 

49 

15 

27 

41 

23 

30 

64 

Attempted household larceny 

Motor vehicle theft 

1 

1 

4 

1 

11 

29 

8 

24 

74 

78 

4 

20 

11 

11 

3 

16 

Attempted motor vehicle theft 1 12 16 62 8 12 5 

Total number 81 197 1,316 1,437 5,892 741 606 57 3 
One would expect, therefore, considerable persons reporting single victimizations. NCS survey procedures separate the resimilarity in the type of crime distributions Actual burglaries fit the opposite pattern, porting and classification of household and 

for the first and second incidents in pairs of being less common among repeat than all person incidents. Whenever a single event 

crime incidents since they can differ only in victims. In the aggregate, crimes against of victimization involves both a household 

the distributions for first and last incidents the household occur only somewhai less and a person crime, e.g., a barglary fob 

in a sequence of victimizations. Any selec- frequently among repeat than among all lowed by a rape, they are reported as two 

tive influence in proneness to type of crime victims while the opposite is the case for separate incidents. Our procedure will err 

for multiple or repeat victimization of a crimes against household members, i.e., in assigning them as separate events in 

household and its members will be re- crimes against persons. time. Moreover, NCS procedures take a 

flected largely in differences between the separate incident report from each member 

distribution for all first reported incidents The degree to which there are switches in of the household who was "robbed, 

and that for the first incident of a pair or 

victimization by type of crime for a house- harmed, or threatened" in the same event. 

the distribution for last reported incidents hold and its members in multiple or repeat Since these incidents are identified only by 

and that for the last incident of a pair or in victimization depends in part upon the sys- month of occurrence, our procedure again tem of classification for crime incidents. differences with the distribution for all re- The procedure followed was to classify will err in assigning them as separate events 

ported victimizations. each crime event by the most serious in time. Although members to a common 

event can be classified in a separatedetailed What is most apparent in Table 1 is the offense reported. A rape with theft, for criine category, e.g., an assault on one and striking similarity in the distributions by example, was classified only as a rape and an attempted assault on the others, in gen- type of crime for all first and last reported not as two separate incidents of a rape and eral such events will contribute dispropor- and all preceding and following incidents theft. Sequences of incidents that occur tionally to the diagonal cells of the crime- of a pair with that for all reported incidents. within the same crime event are thus ex- switch matrix. Relative to the aggregate of Although this similarity is determined to cluded from the crime-switch matrix. all multiple victimization over time, these 

some degree by the relative frequency of events are relatively uncommon so that the 

types of crime among all victimizations, it amount of error should be small. These is apparent that multiple or repeat victims sources of error could be eliminated were of households aregenerally no more or less NCS procedures to clearly separate inciprone to victimization by certain types of dents that occur in the same event in time 

crime than are all victims. There are some from those that do not and also identify exceptions. Assaulp, particularly attempted members of the household to a common assaults, occur more frequently among event.

repeat than among all victims and by deduction they occur less commonly among 

Number of crime incident pairs of preceding and following detailed major types of crime reported by a household and 

its members: All households reporting two or more victimizations while in survey, July 1, 1972, to 

December 31, 1975 

Type of crime reported as following inciderit 

Per- House- Per- House- hold Att. Att. Att' Bur- Bur- Att. sonal per- house- motor Total

purse sonal larceny sonal glary, glary, no bur- larceny hold larceny under vehicle vehicle number 


Inat* $50+ S50 larceny force force glary la;;: u;~ larceny theft theft 


7 16 5 2 4 2 9 1 3 77 

3 11 43 5 7 8 13 7 27 2 5 3 196 

2 100 233 26 78 92 53 68 145 16 32 8 1,346 

4 93 315 30 64 83 32 82 163 16 25 12 1,473 

3 371 1,244 141 196 301 184 230 557 72 87 52 5,767 

1 76 130 21 41 54 23 41 78 5 15 13 799 

55 156 21 26 37 16 27 63 7 13 6 649 

4 48 141 22 38 42 26 30 48 8 17 15 61 0 

10 9 18 5 4 4 1 3 10 2 6 93 

9 859 1,385 173 231 337 159 317 544 55 133 7 1 5,054 

13 1,428 7,067 474 436 960 363 637 1,749 158 247 168 15,999 

4 156 446 149 53 72 47 68 142 19 35 33 1,463 

4 212 450 53 666 237 198 183 394 53 79 31 3,026 

7 354 917 74 258 993 134 253 550 58 88 38 4,375 

151 395 43 192 172 360 116 327 39 33 32 2,194 

4 350 636 65 179 261 121 475 552 68 82 48 3,311 

14 544 1,779 133 378 597 297 555 2,526 171 149 81 8,234 

2 65 161 24 33 49 47 62 164 73 16 15 827 

2 134 253 25 74 76 48 74 127 8 122 28 1,151 

1 77 156 33 36 40 27 39 96 23 36 83 763 

87 5,100 15,941 1,517 2,995 4,417 2,153 3,269 8,271 854 1,223 737 57,407 i 

> 
The crime-switch matrix in Tables 2-5 pre- matrix. The reader is cautioned, in any most likely events. The other major crimes 

sents shifts in type of crime for repeat or case, against interpreting the ordering of against persons or households occur much 

multiple victimization of households re- personal crime incidents as applying to the less frequently: motor vehicle theft (3 perporting two or more victimizations between same person. cent); robbery (2 percent); purse-snatching 

July 1, 1972, and December 31, 1975. The or pocket-picking (l percent); and the least 

matrix is presented in two different ways. Observed switches in type of crime frequent, rape (0.4 percent). Yet, amongreTable 2 presents the frequency distribution peat victims, given prior victimization by 

for the crime-switch matrix. Table 3 dis- of a household and its members 

in repeat victimization one of the most frequently occurring 

plays the percent of each type of crime that crimes (assault, personal larceny without 

follows a preceding reported type of crime There is considerable mutliple and repeat contact, household larceny, and burglary). 

in a sequence of eight major types of crimes victimization by crime. The longer the time the most likely next victimization is by the 

against households and persons. interval for which victimization is meas- same type of crime. Roughly a third of all - -- -... - - --- ured, the greater the propensity to repeat assaults and of all burglaries, 38 percent of The reader sho~ld bear in mind that these .victimization. all household larcenies and 54 percent of all 

reports of victimization are for a household personal larcenies are preceded and fol- and its members. Where crimes against Given the distribution of all reported vicpersons are involved, the two incidents in a tim incidents or of that for repeat victims lowed by reports of victimization by that 

pair might be for the same or for different only (Table l), the most likely victimiza- same type of crime (Tables 2 and 3). In remembers of the same household. Thus, a tion by a major type of crime is a personal peat victimization for the less frequently 

occurring crimes (motor vehicle theft, rob- robbery followed by robbery could be re- larceny (39 percent) with household lar- bery, purse-snatching or pocket-picking, ported for the same or for different mem- ceny (22 percent), burglary (17 percent) and rape), the most likely next victimiza- bers of the same household. Unfortunately, and assault (15 percent) among the next tion is the most frequently occurring crime 

we are unable to distinguish victims within of personal larceny without contact. the same household to a common event, Roughly 3 in 10 of these less frequently e.g., an assault, and our procedure for occurring crimes are followed by a per- ordering events will treat them as separate sonal larceny (Table 2). victimizations occurring at different, though 

closely related, points in time. There is, 

therefore, a conf9unding of some preceding and following events in the crime-switch 

Table 2b. 

Purse Type of crime Att. Serious Minor Att. Att. snatch, preceding next Rape rape assault assault assault robbery pocket reported type of crime picking 

Rape 7.8 3.9 10.4 1.3 6.5 2.6 2.6 1.3 

Attempted rape 0.5 8.2 3.1 4.6 10.7 0.5 3.1 1 .O 

Serious assault 0.2 0.8 8.8 5.6 15.8 2.8 1.4 1.3 

Minor assault 0.3 0.5 5.6 10.3 16.6 1.6 1.4 1.4 

Attempted assau It 0.2 0.5 3.5 4.0 29.2 1 .O 1.4 0.6 

Robbery 0.3 0.5 6.3 3.7 9.5 11.1 3.4 2.9 

Attempted robbery 0.2 0.8 4.6 3.2 11.1 4.2 8.3 1.9 

Pcrse snatchinglpocket picking 0.2 0.3 3.4 3.1 7.7 4.3 1.5 7.5 

Attempted purse snatching - 3.2 2.1 10.8 2.1 3.2 1.1 

Personal larceny, $50 and over 0.1 0.3 2.2 2.0 7.9 1.2 0.9 0.9 

Personal larcency, under $50 0.1 0.2 1.5 1.8 8.2 0.8 0.9 0.9 

Attempted personal larceny 0.1 0.2 1.7 2.3 7.9 1.5 1.6, 1 .O 

Burglary, forced entry 0.2 0.6 3.0 2.0 6.6 1.4 0.8 0.9 

Burglary, no forcible entry 0.2 0.2 1.9 2.4 7.3 1 .O 0.8 0.9 

Attempted burglary - 0.4 2.1 2.1 7.6 1.4 0.7 1 .O 

Household larceny, $50 and over 0.1 0.2 1.9 1.8 7.2 1.3 0.7 0.9 

Household larceny, under $50 0.1 0.2 1.1 1.9 627 0.9 0.6 0.8 

Attempted household larceny 0.1 0.5 1.3 1 .O 9.0 0.5 1.3 0.4 

Motor vehicle theft 0.1 0.1 2.5 2.1 6.8 1.7 1 .O 1.4 

Attempted motor vehicle theft - 0.1 1.6 2.1 8.1 1.1 1.6 0.7 

All next reported incidents 0.1 0.3 2.3 2.5 10.3 1.3 1.1 1 .O 

Number next reported incidents 81 197 1,316 1,437 5,892 741 606 573 

I No incidents reported 
- -- 

Table 3. Percent distribution by next reported type of crime for major preceding types of crime reported by households with two 

or more victimizations of the household and its members: All household and person victimizations, July 1,1972, 

to December 31,1975 

I 	 Next reporredVpe of crimeg Total 

Type of crime? D,.rrs I

preceding next I "IS Motor I reported crime Rape Assault Robbery ~~~~~~'Burglary larQny vehicle Percent Number I ~~~~~; 

nirkinn 	 theft 

Rape 9.5 


Assault 0.8 


Robbery 0.8 


Purse snatching, pocket picking 0.4 


Personal larceny 0.3 


Burglary 0.5 


Household larceny 0.3 


Motor vehicle theft 0.2 


Total 	 0.5 15.1 2.3 1.1 39.3 16.7 21.6 3.4 100.0 57,407 

'AII types of crime include both actual and attempted crimes. 

There is considerable variation in patterns of all reported victimizations. 9 percent of Since rape is a form of assault, some 

of repeat victimization for the different all rapes occurring in households reporting interest attaches to victim proneness to 

major types of crime, however, as the fol- two or more victimizations were followed rape and other types of assault (serious, 

lowing summary based on Tables 2 and 3 by a rape. There appear to be differences in minor, and attempted assault). Somewhat 

discloses. victim proneness to actual and attempted more rapes than expected in households 

(I) Despite the fact that rape is an infre- rape. Most rapes preceded or followed by reporting two or more victimizations were 

quent event accounting for only 0.4percent an attempted rape are also attempted 

tapes, and a substantial majority of rapes 

preceded or followed by an actual rape are 

actual rapes. 

Percent distribution by next reported type of crime for major preceding types of crime reported by households 

with two or more victimizations of the household and its members: All household 

and person victimizations, July 1, 1972, to December 31, 1975 

Next reported type of crime 

Per-	 House- Att. Att. Bur- House-	 Att. Att. Per- sonal per- Bur- Att.

Iaz:' 	 hold house- motor Total purse larceny, glary, bur- holdlarceny hold vehicle 


match under sonal no larceny under
 $50 larceny force force glary $50+ larceny theft theft 

9.1 20.8 6.5 2.6 5.2 2.6 11.7 1.3 3.9 100.1 

1.5 5.6 21.9 2.6 3.6 4.1 6.6 3.6 13.8 1.O 2.6 1.5 100.1 

0.2 7.4 17.3 1.9 5.8 6.8 3.9 5.0 10.8 1.2 2.4 0.6 100.0 

0.3 6.3 21.4 2.0 4.3 5.6 2.2 5.6 11.1 1.1 1.7 0.8 100.0 

0.1 6.4 21.6 2.4 3.4 5.2 3.2 4.0 9.7 1.2 1.5 0.9 100.0 

0.1 9.5 16.3 2.6 5.1 6.8 2.9 5.1 98 0.6 1.9 1.6 100.0 

8.5 24.0 3.2 4.0 5.7 2.5 4.2 9.7 1.1 2.0 0.9 100.1 

0.7 7.9 23.1 3.6 6.2 6.9 4.3 4.9 7.9 1.3 2.8 2.5 100.1 

10.8 9.7 19.3 5.4 4.3 4.3 1.1 3.2 108 2.1 6.5 100.0 

0.2 17.0 27.4 3.4 4.6 6.7 3.1 6.3 10.8 1.1 2.6 1.4 100.1 

0.1 8.9 44.2 3.0 2.7 6.0 2.3 4.0 10.9 1.O 1.5 1.0 100.0 

0.3 10.7 30.5 10.2 3.6 4.9 3.2 4.7 9.7 1.3 2.4 2.3 100.1 

0.1 7.0 14.9 1.8 22.0 7.8 6.5 6.0 13.0 1.8 2.6 1.0 100.0 

0.2 8.1 21.0 1.7 5.9 22.7 3.1 5.8 12.6 1.3 2.0 0.9 100.0 

6.9 18.0 2.0 8.7 7.8 16.4 5.3 14.9 1.8 1.5 1.4 100.0 

0.1 10.6 19.2 2.0 5.4 7.9 3.7 14.3 16.7 2.0 2.5 1.5 100.0 

0.2 6.6 21.6 1.6 4.6 7.2 3.6 6.7 30.7 2.1 1.8 1.0 100.0 

0.2 7.9 19.5 2.9 4.0 5.9 5.7 7.5 19.8 8.8 1.9 1.8 100.0 

0.2 11.6 22.0 2.2 6.4 6.6 4.2 6.4 11.0 0.7 10.6 2.4 99.9 

0.1 10.1 20.5 , 4.3 4.7 5.2 3.5 5.1 12.6 3.0 4.7 10.9 100.0 

0.1 	 8.9 27.8 2.6 5.2 7.7 3.8 5.7 14.4 1.5 2.1 1.3 100.0 


87 5,100 15,942 1,517 2,995 4,417 2,153 3,269 :8,271 854 1,223 737 57,407 


-

followed (18 percent) by an assault. Of 

some interest also is the fact that actual 

rapes were far more likely than expected to 

occur in households that next reported a 

serious assault (10 percent). 

(2) Repeat victims are only slightly 

more prone to assault than are victims reporting only a single victimization. For 

households reporting two or more victimizations, 15 percent of all victimizations 

were an assault while about 13 percent of 

all single victims reported an assault. 

There is substantialproneness to assault 

among victims reporting an assault. Given 

the occurrence of an assault on a household 

member, 35 percent of all preceding and 

following incidents reported for the household are an assault. Serious and minor 

assaults were about as likely to be followed 

by a serious or minor as by an attempted 

assault, but attempted assaults followed by 

an assault are ordinarily followed by an 

attempted assault. 

(3) Repeat victims are only slightly 

more prone to robbery than aresingle-time 

victims. Of all reported victimizations, 2.1 

percent are robberies while 2.4 percent of 

all incidents reported by multiple victimized households are robberies. 

There is substantial proneness to robbery among victims of robbery. Given the 

relatively low probability of a robbery, a 

substantially greater proportion (14 percent) of all robberies reported against 

household members in households with 

two or more victimizations were preceded 

or followed by a robbery of a member. 

Moreover, actual robberies are generally 

preceded and followed by actual robberies 

and attempted by attempted robberies. 

Among repeatedly victimized households reporting robbery, their risk of 

repeat victimization by robbery is less than 

their risk of victimization by the major 

crimes of personal larceny without contact 

(32 percent) or assault (19 percent), but 

about the same as that for the much more 

frequently occurring crimes of burglary 

and household larceny. 

(4) Purse-snatching and pocket-picking 

are relatively infrequent events accounting 

for only 1.4 percent of all crime incidents 

reported in the victim survey and an even 

smaller proportion of those for multiple 

victimized households (1.1 percent). Yet, 

much as in the case for the infrequent event 

of rape, there is considerable proneness to 

repeat victimization among those victimized by purse-snatching or pocket-picking; 

9 percent of all purse-snatching or pocketpicking incidents were followed by some 

member of the household reporting the 

same kind of victimization. There is a 

strong tendency for reports of actual to be 

followed by actual purse-snatching or 

pocket-picking and attempted to be followed by attempted purse-snatching or 

pocket-picking. 

Among repeat victim households reporting a purie-siatching or pocket-pickikg by 

one of their members. the risk of victimization is greatest for personal larceny without 

contact (35 percent), with burglary, household larceny, or assault being equally likely 

as next reported events. 

(5) There is considerable victim proneness for victims ofpersonal larcezy without 

contact. Although personal larceny without contact is the most frequently occurring 

major crime against a household and its 

members accounting for 39 percent of all 

victimizations, 54 percent of all personal 

Table 4. 

Type of crime Rape reported as 

preceding incident and Serious Minor Att. 

att. assault assault assault Robbery 

rape 

Rape and attempted rape +461 +10 +1 -* -* 

Serious assault +6 +252 +51 +40 +22 

Minor assault +3 +72 +360 + 57 +* 

Attempted assault -5 +34 +49 +2019 -3 

Robbery -* +600 

Attempted robbery +l +55 +51 +* +41 

Purse snatchlpocket picking -*+3 +I5+4 +1 -3 +39 

and attempts 

Personal larceny, $50and over -+ -* -6 -27 -* 

Personal larceny, under $50 -11 -45 -29 -65 -32 

Attempted personal larceny -1 -2 -* -8 +* 

Burglary, forced entry +6 +6 4 -40 +* 

Burglary, no force -* -2 -* -38 -2 

Attempted burglary -1 -* -1 -1 6 +* 

Household larceny, $50and over -1 -3 -6 -31 +* 

Household larceny, under $50 -6 53 -13 -100 -9 

Attempted household larceny +* -3 -8 -1 -4 

Motor vehicle theft -2 +* -1 -1 4 +3 

Attempted motor vehicle theft -2 -2 -* -3 -* 

Rape and attempted rape 2.6 

Serious assault 1.4 

Minor assault 2.1 

Attempted assault 11.6 

Robbery 3.4 

Attempted robbery 

Purse snatchlpocket picking 

and attempts 


Personal larceny, $50and over 


Personal larceny, under $50 


Attempted personal larceny 


Burglary, forced entry 


Burglary, no force 


Attempted burglary 


Household larceny, $50and over 


Household larceny, under $50 


Attempted household larceny 


Motor vehicle theft 


Attempted motor vehicle theft 

x2 = 17,461;d.f. = 289 

* = less than .5 

+ = Observed > expected frequency; -= < expected frequency. 


Goodmen-Kruskal Index (0) .20 * .004. 


< 
larcenies without contact were followed by 

that same type of crime. Major ($50 or 

more), minor (under $50) and attempted 

personal larcenies without contact are all 

most likely to be followed by a minor personal larceny without contact in repeat 

larceny victimization. Nonetheless, a major 

personal larceny is more than twice as 

likely ta be followed by another major personal larceny as would be expected from 

the risk of major personal larceny for all 

victims. 

Minor personal larcenies show thegreatest propensity to repeat victimization by 

minor personal larceny and are less likely 

than the other types of personal larceny 

without contact (major and aiiempted) to 

be followed by an attempted or major personal larceny. This propensity perhaps reflects differences in the victim composition 

of larceny victims by type of larceny. A 

substantial number of minor personal larcenies involve school-age victims where 

repeat victimization involves minor personal larcenies at school. 

(6) There is likewise considerable victim 

proneness among victims of burglary. 

About a third of all burglaries of households reporting two or more victimizations 

were preceded or followed by a burglary. 

Attempted burglaries were about as 

likely to be followed by an actual as an 

attempted burglary but actual burglaries 

with or without force were quitelikely to be 

Actual and percent cell contribution to chi square of pairs of victimizations in a crime-switch matrix 

for repeat household victims of detailed person and household crimes: All household 

and person victim@ations for households reporting two or more victimizations, 

July 1,1972, to December 31,1975 

Type of crime reported as following incident I 

Purse per- Per- Att. Bur- Bur- House- Att. 

Att. snatch, sonal sonal Att. House- hold house- larceny, per- glary, glary, bur- larceny, motor robbery larceny, under sonal forced no hold vehicle vehicle 

plcklng $50+ larceny, under 

and att. $50 larceny entry force 'Iary $50+ $50 larceny theft theft 
1 Table 5. Actual and percent cell contribution of chi square of pairs of victimizations in a crime-switch matrix for repeat household 

victims of major household and person crimes: All household and person victimizations for households reporting two or more 

victimizations, July 1,1972, to December 31,1975 

Type of crime 

reported as 

preceding incident 

Rape

Assault 

Robbery 

Purse snatching, pocket picking 

Personal larceny, without contact 

Burglary

Household larceny 

Motor vehicle theft 

Rape 

Assault 

Robbery 

Purse snatching, pocket picking 

Personal iarcenv. . . without contact 

Burglary 

~ousehold larceny 

Motor vehicle theft 

Type of crime reported as following incident I 

Purse Personal 

$g:lt Motor 

Rape Assault Robbery sn~~~~g' Burglaw vehicle 

theft picking contact 

-* t460 +3 -3 -6 -1 -2 

+13 i2.246 +2 +7 -2 -200 -84 +I37 -20 

+4 +17 t782 +22 -21 --8 -27 -I 

-8 -* +33 t346 --4 -* -1 7 +8 

-1 1 -172 -25 -3 + 1,223 -319 -283 --9 


+1 -74 -5 -1 -334 +1,624 -5 -2 


-5 -201 -25 -251 -5 +1,460 -2


4 -1 6 +1 3 -7 -1 -5 +635 

Percent of total chi square I 

4.1 


20.1 


7.0 


3.1 

1.5 


1.8 1.2 


10.9 2.8 2.5 


I 

where the observed frequency is substantially greater than the expected frequency. 

Indeed, the diagonal cells in Table 4 

account for 78.1 percent of the total value 

of chi-squared and in Table 5, for 78.4 percent. We can conclude then that the 

chances a household or one or more of 

its members will be successively victimized 

by the same type of crime are greater than 

one w~ould expect given the chance aN 

households and their members have of 

being victimized by that type of crime. By 

this measure, then, in repeat victimization. 

there is household victim proneness to the 

same type of crime. The chances of next 

being victimized by a robbery, for example, 

are greater if the previous victimization 

was a robbery than if it was some other type 

of crime. 

Readers should take note that proneness to 

victimization by the same type of crime 

does not predict the most likely next victimization by a major type of crime. That 

is, proneness to victimization by the same 

type of crime does not say that whenever a 

household or one of its members is victimized by any major type of crime, it has a 

greater chance of next being victimized by 

the same rather than by some other type of 

crime. The chances that a victim of a rob- 

*Less than .5 

+ = Observed >exuected freauencv 

followed by the same kind of actual burglary. Thus, 22 percent of all actual burglaries with force were followed by an 

actual burglary with force compared with 8 

percent followed by burglary with no force 

and 7 percent followed by attempted burglary. Similarly, 23 percent of all actual 

burglaries without force were followed by 

an actual burglary without force compared 

with 6 percent followed by an actual 

burglary with force and 3 percent followed 

by attempted burglaries. 

(7) Households victimized by household larceny are prone to repeat victimization by household larceny. While 22 percent of all households reported a household larceny, 38 percent of all households 

victimized by household larceny reported a 

preceding or following incident of household larceny. As for personal larceny, any 

household larceny followed by a household 

larceny is most likely to be a minor household larceny with a loss of $50 or less. But a 

substantially greater proportion of major 

household larcenies ($50 and over) are followed by a major household larceny than 

expected. A similar pattern holds for 

attempted household larcenies. 

(8) Motor vehicle theji victims also 

show a propensity to repeat victimization 

by the same type of crime. This propensity 

holds for both attempted and actual motor 

vehicle theft. As for other infrequently 

occurring crimes, motor vehicle theft is 

most likely to be preceded or followed by a 

personal larceny without contact but the 

x2 = 11,190;d.f. = 49;Goodman-Kruskai Index (G) = .26f .005. 

other mqjor types of crimes are about as 

likely events as is motor vehicle theft in 

their repeat victimization. 

This brief description of victim proneness 

in repeat victimization of a household and 

its members has emphasized the proneness 

to repeat victimization by the same type of 

crime despite substantial differences in the 

probability of victimization among the 

types of crime. The test of proneness has 

been the departure of these patterns from 

expected frequency of occurrence, given 

the distribution of types of crime among all 

repeat victimized households. The test of 

divergence between the actual crime-switch 

matrix and an expected one based on the 

types of crime reported by repeat victims 

used was the chi-square test for homogeneity of proportions. The chi-square test for 

an 18 by 18 detailed type of crime matrix is 

presented in Table 4 and for an 8 by 8 major 

type of crime matrix in Table 5. 

Given the substantial number of pairs, 

57,407, in the matrices, the chi-square is 

expected to be significant. Our attention in 

these tables, therefore, focuses on the cells 

in the crime-switch matrix that contribute 

significantly to the chi-squared. 

The diagonal cells in Tables 4 and 5 are 

those where the same type of crime is repoited in a pair. Each of these cellscontributes significantly to the value of chi-squared 

and they are the only cells in these tables 
bery or a motor vehicle theft will next be 

victimized by a personal larceny are greater, 

for example, than victimization by the 

same type of crime. Rather, for any major 

type of crime, the chances of next beingvictimized by any major type of crime are 

greater than chance only for the same type 

of crime. 

There are eight cells in Table 5 where the 

observed frequency of pairs is significantly 

less than expected, given the type of crime 

distribution for all multiple victimized 

households and their members. These cells 

account for an additional 16.8 percent of 

the total value of chi-squared or all but 5 

percent of the remaining variance. They involve selected combinations among the four 

most frequently occurring crimes of personal and household larceny, burglary, and 

assault. The eight cells can be regarded as 

four symmetrical pairs with (1)assault with 

personal larceny, (2) assault with household larceny, (3)personal larceny with burglary, and (4) personal larceny with household larceny occurring less frequently than 

expected. Thus an assault, for example, is 

less likely to be followed by a personal larceny than expected and a personal larceny 

is less likely to be followed by an assault 

than expeAed. Just why multiple victimized households and their members should 

be less prone to these four symmetrical 

patterns of victimization is not apparent. 

All other pairs of victimization by type of 

crime occur about as often as expected. A 

rape followed by an assault or an assault 

followed by a rape, for example, occurs 

about as often as expected. 

When examining the effect that victimization by a type of crime has on the chances 

of victimization by any other type of crime 

in repeat victimization, the question arises 

whether the order of victimization by a 

type of crime has an effect. Such effects 

could be presumed to occur were victims to 

alter substantially their behavior to avoid 

repeat victimization by a serious type of 

crime, and take precautions that reduce the 

likelihood of victimization by even less 

serious types of crime which would not be 

taken were one previously victimized by 

the less serious crime. Thus, if one or more 

household members were victimized by 

robbery, the propensity tostay home might 

reduce the risk of it being followed by a 

robbery. 

An answer to the question of the effect of 

prior or subsequent victimization by type 

of crime is provided by examining the extent of symmetry in paired victimizations 

by type of crime. When any two types of 

crime are paired by their order of occurrence, the pairs aresymmetrical if the probability of their occurrence is the same and it 

differs from other crime pairs. Even if the 

full conditions of symmetry are not met but 

the probability of occurrence remains the 

same for paired orders, there would be little 

evidence that prior victimization has had a 

substantial effect on type of crime victimization in repeat victimizafion. 

Among the 12 person and 8 household 

detailed types of crime in Table 2 that can 

be reported as victimizations by households 

and their members reporting two or more 

victimizations, there are 400 possible pairs 

of incidents by type of crime when each incident is paired with the next succeeding incident by type of crime. Twenty of these 

pairs occur when the same type of crime is 

reported for two consecutive incidents. The 

remaining 380 pairs of consecutive incidents could comprise 190 symmetrical 

pairs. Similarly, among the five person and 

three household major types of crime in 

Table 3, there are 64 possible pairs of incidents; eight of these occur when the same 

type of crime is reported for two consecutive incidents. The remaining 56 pairs of 

consecutive incidents could comprise 28 

symmetrical pairs. When the 400 and the 64 

pairs are ordered by their actual rate of 

occurrence among 10,000 pairs among 

households reporting two or more victimizations, the order of occurrence ofa type of 

crime in a pair has little effect on theprobability of occurrence of a pair. One of the 

conditions of symmetry with respect to pair 

order thus is satisfied; any two types of 

crime have essentially the same probability 

of occurrence regardless of the order of victimization. For example, the probability of 

a household larceny less than $50 being 

followed by a personal larceny less than 

$50 is 310 in 10,000 pairs, while it is 305 for 

a personal larceny less than $50 being followed by a household larceny less thanS50. 

There is no evidence then that victims or 

offenders have any effect on the order of 

victimization by different types of crime for 

repeat victimization. Where there is repeat 

victimization by the same type of crime, 

however, it is quite possible that victims 

and offenders have an effect, given their 

significant departure from chance occurrence. 

The second condition for symmetry is that 

the probability of any two pairs that differ 

only by order of occurrence differ from 

that of all other pairs. This condition of 

symmetry is more or less satisfied for major 

types of crime though it is less apparent for 

many of the pairs for detailed types of 

crime. Generally, however, there is symmetry in the pairs involving major crimes 

against .persons and households.2 

There is considerable variation, however, 

in the probability that any two types of 

crime incidents will be consecutive victimizations. The probability of consecutive victimization by the same type of crime varies 

directly with the probability of occurrence 

of that type of crime among all victims. 

Moreover, the greater the probability of 

victimization by any type of crime, the 

more likely it is to occur in consecutive victimization with any other type of crime. 

Switches in type of household 

crime in repeat victimization 

of households 

We shall next consider briefly the household as the unit at risk in repeat victimization for household crimes only-those of 

burglary, household larceny, and motor 

vehicle theft. In general, repeat victims of 

household crimes are no more or less prone 

to victimization by certain household 

crimes than are all victims (Table 6). Motor 

vehicle theft may occur somewhat less 

often amongrepeat than among all victims, 

but the difference is very small. 

Among major crimes against households, 

the most likely household victimization is 

that of household larceny (52 percent) with 

burglary somewhat less common (40 percent) and motor vehicle theft least common 

(8 percent). Actual household crimes occur 

with greater frequency than do attempted 

ones. Attempted household crimes are particularly un;ommon for household larEeny 

where only about I in 14 household larcenies is reported as an attempt. The comparable odds for burglary are that 1 in 4 is an 

attempt while almost 1 in 3 motor vehicle 

thefts is an attempt. The odds areabout the 

same for repeat as for all victims during the 

three and one-half years for which victimization was reported. 

?A more succinct test for symmetry is presented in the 

companion paper by Fienberg. 
Table 6. Percent of each type of crime for order of reporting household victimizations: All household victimizations, July 1,1972, 

to December 31,1975 

Type of 

household crime 

Burglary, forced entry 

Burglary, no force 

Attempted burglary 

Household larceny, $50and over Household larceny, under $50 

Attempted household larceny 

Motor vehicle theft 

Attempted motor vehicle theft 

Totals 

Order ,of reporting victimization 

Reported as Reported as Reported as Reported as preceding following first last incident incident incident incident of a air of a pair 

Number Percent Number Percent Number Percent Number Percent 

4,140 12.7 4,102 12.6 2,257 13.4 2,215 13.1 

5,978 18.3 6,005 18.4 3,062 18.1 3,087 18.3 

2,914 8.9 2,891 8.9 1,565 9.3 1,541 9.1 

4,359 13.4 4,323 13.2 2,295 13.6 2,262 13.4 

11,387 34.9 11,403 34.9 5,881 34.8 5,889 34.9 

1,107 3.4 1,I 26 3.4 587 3.5 606 3.6 

1,740 5.3 ' 1,816 5.6 740 4.4 816 4.8 

999 3.1 970 3.0 497 2.9 468 2.8 

32,624 100.0 32,636 100.0 16,884 100.0 16,884 100.0 

All 

reported 

incidents* 

Number Percent 

6,362 12.8 

9,074 18.3 

4,458 9.0 

6,621 13.4 

17,286 34.9 

1,713 3.4 

2,562 5.2 

1,469 3.0 

49,545 100.0 

*The entries for "Reported as first incident" and "Reported as following incident of a pair" do not always sum to the total, "All 

Reported Incidents," for each type of crime because there are 37 incidents for which month of occurrence is unreported. 

There is some variation in patterns of 

repeat victimization for the different 

detailed and major types of household 

crime (Table 7). 

There is substantial proneness to repeat 

victimization by the same major type of 

household crime. While the odds of household larceny are roughly 5 in 10 for all 

household victims, they rise to between 6 

and 7 in 10 for households previously victimized by a household larceny. Similarly, 

while the burglary odds are 4 in 10 for all 

household victims, they are almost 6 in 10 

for households previously victimized by 

burglary. The odds for victimization by 

motor vehicle theft are less than I in 10 for 

all victimized households, but almost 3 in 

10 when a motor vehicle theft is previously 

reported. 

Regardless of the type of burglary, the odds 

are that the next household victimization 

will be a burglary. There is, moreover, a 

substantial propensity for victimization by 

the same type of burglary. The same 

pattern holds for household larceny. For 

motor vehicle theft, however, the odds are 

that the next victimization will be a house- 

'hold larceny or burglary, though there is 

nonetheless a substantial propensity for repeat victimization by motor vehicle theft. 

The odds on repeat victimization by motor 

vehicle theft are four times greater for those 

previously victimized by motor vehicle 

theft than they are for all household victims 

and more than seven times greater for 

attempted motor vehicle theft. 

The chances that a household will be victimized by the same type of household 

crime, then, are substantially greater than 

one expects given the chances all households have for victimization by that type of 

crime. Further evidence for this is found in 

Table 8. The propensity to repeat victimization by the same type of crime (stayer or 

diagonal cells in Table 8) is substantial. 

These are the only cells where the observed 

frequency is signficantly greater than the 

expected and they account for 81 percent of 

the variance in chi-squared for repeat victimization by detailed types of crime and 68 

percent of the variance in major types of 

crime. One other pattern is worth noting. 

Actual burglaries-occur significantly leis 

often with actual household larcenies than 

one would expect given the chances of victimization for all households. This is surprising given the close relationship between 

the two types of crime and the possibilities 

for misclassification. 

As one might expect from the substantial 

differences in the probability of victimization among different types of household 

crimes, there is considerable variation in 

the probability that any two types of household crime will be consecutive victimizations. The probability of consecutive victimization by the same type of household 

crime generally varies directly with the 

probability of occurrence of that household crime among all victims. Moreover, 

the greater the probability of victimization 

by any type of household crime, the more 

likely it is to occur in repeat victimization 

with every other type of household crime. 

For every major type of household crime 

also, the probability that it will occur consecutively in repeat victimization with any 

other type of crimes is a function of their 

joint probability of victimization. That is, 

excluding victimization by the same type of 

crime, for every major type of household 

crime, the probability that it will occur with 

every other major type of household crime 

in repeat victimization varies directly with 

their expected probability of occurrence 

based on the experience of all victims. 

Conclusion 

Within a population of victims, there is 

considerable multiple or repeat victimization. Evidence on repeat victimization 

makes it clear that victimization is not a 

random occurrence but that there is proneness to repeat victimization. Moreover, in 

repeat victimization, there is a proneness to 

repeat victimization by the same type of 

crime. Apart from a marked proneness to 

victimization by the same type of crime in 

repeat victimization, most patterns of victimization by type of crime in repeat victimization occur about as often as 

expected. 

The order of occurrence of a type of crime 

in a pair has little effect on the probability 

of occurrence of a pair. There is, moreover, 

a general symmetry in the pairs involving 

major types of crimes against persons and 

households. The probability of consecutive 

victimization by the same type of crime 

varies directly with the probability of 

occurrence of that type of crime among all 

victims. The greater the probability of victimization by any type of crime, the more 

likelv it is to occur in consecutive 

victimization with any other type of crime. 

Reference 

Dodge, Richard W. (1975) 

National Crime Survey: Comparison of victimizations as reported on screen questions with 

their ,final class~fication. 1974. Washington, 

D.C.: U.S.Bureauof thecensus Memorandum, 

December 1, 1975, p. 5. 
# 

Table 7. Percent distribution by next reported for precedingdetailed and major types of householdcrime for households reporting two or more householdvictimizations: All householdvictimizations, July 1, 1972, to December 31, 1975' 

I Percentdistribution by following detailed type of household crime I I 

Type of crime reported as following incident 

Total I 

Type of crime House- House- Att. 

reported as hold hold Att. Total Motor nrotor preceding 

preceding incident An' larceny larceny h:i7- vehicle vehicle incidents 

force brce burg'aw S5Oand under 

over $50 theft theft 

Burglary, forced entry 34 14 11 10 22 3 5 2 

Burglary, no force 11 39 6 11 25 2 4 2 

Attempted burglary 15 13 26 9 28 3 3 3 

Household larceny, $50 and over 10 15 7 26 30 4 5 3 

Household larceny, under $50 8 13 6 12 51 4 4 2 

Attempted household larceny 7 12 10 15 36 14 3 3 

Motor vehicle theft 13 14 9 14 23 2 20 5 

Attempted motor vehicle theft 9 11 8 10 25 5 10 22 

All next reported incidents 13 18 9 13 35 4 5 3 100 16,884 

Percent distribution by following major type of householdcrime 

Type of crime reported 

as following incident Total 

Type of crime 

reported as 

precedingincident Household 2:;:; Number of 

Burglary Percent preceding 

larcenytheft incidents 

Burglary 57 

Household larceny 29 

Motor vehicle theft 32 

All next reported inclden~s 40 52 8 100 16,884 

I Table 8. Actual and percent cell contribution to chi square of pairs of household crimes in a crime-switch matrix for repeat household 

victims of crime: All detailed household victimizations. Julv 1.1972 to December 31 1975 1 

I - -

Type of household crime reported as following incident 

Tvm of -1 

house6bldceime Burglary, Bu:Fyl Household Household Attempted Motor Attempted reported as 

precedingincident forcible forcible I~$~~' household vehicle :;iL 

entry entry over $50 larceny theft theft 

Burglary, forcible entry Burglary, no forcible entry Attempted burglary 

Household larceny, $50 and over Household larceny, under $50 

Attempted household larceny 

Motor vehicle theft 

Attempted motor vehicle theft - - --

I Percent of total chi square 

Burglary, forcible entry 15.5 2.2 

Burglary, no forcible entry 15.6 2.0 

Attempted burglary 10.7 

Householdlarceny, $50 and over 5.3 

Household larceny, under $50 2.4 1.7 9.2 

Attempted household larceny 3.7 

Motor vehicle theft 7.7 

Attempted motor vehicle theft 13.7, 

x2 = 4,826; d.f. = 49; Goodman-Kruskal Index = .22 * .008. 

Less than .5 
Statistical modelling in the analysis 


of repeat victimization 

STEPHEN E.F~ENBERG 

Department of Statistics 

and Department of Social Science 

Carnegie-Mellon University 

The National Crime Survey's panel structure allows for the longitudinal analysis of 

individual victimization records. In this 

paper, further details are provided on a 

semi-Markov model for such longitudinal 

analysis proposed in Fienberg (1978). The 

'relationship between this model and some 

analyses of Reiss (1980) on data for repeat 

victimization are noted. Finally, Reiss's 

.data are reanalyzed using a variety of loglinear models. The resulting models are interpreted in the context of victim vulnerability or proneness. 

1. Introduction, 

The National Crime Survey (NCS) has a 

longitudinal structure that potentially 

allows for the analysis of individual and 

household victimization records over time. 

In particular, this longitudinal structure 

can be used for the examination of the 

extent of repeat victimization, and for an 

explorat!on of the concept of victim proneness. Fienberg (1978) briefly outlined a 

~ro~osal for the use of a semi-Markov 

*oiel for multiple victimization over time. 

In Section 2 of this paper we give more details for this model and point out some of 

its implications for the analysis of longitudinal victimization records. This paper 

presumes a knowledge of various concepts 

and phenomena related to the NCS and 

victimization surveys, as presented e.g., by 

Fienberg (1978) or Penick and Owens 

(1976). 

An interesting and well-known consequence of the .use of the semi-Markov 

model of Section 2 is the separation, for 

estimation purposes, of the transitions 

from one victimization to subsequent ones, 

from the timing of the victimizations (i.e., 

information on the inter-victimization time 

intervals). If the Markov-chain component 

of the semi-Markov process is of order one, 

then we only need to examine a one-step 

transition matrix for repeat victimization. 

Thus a version of the model of Section 2 is 

consistent with the analysis of the crimeswitch matrix presented by Reiss (1980) in 

the preceding paper. The link between 

Reiss's approach and the use of semiMarkov models is outlined in Section 3. 

Then in Section 4 we present a reanalysis of 

Reiss's crime-switch matrices using multiplicative (or loglinear) models of the sort 

discussed in Bishop, Fienberg, and Holland 

(1975). This method of analysis leads to a 

more systematic exploration of patterns of 

repeat victimization and risk than has been 

proposed to date. The results of our reanalyses lead to a somewhat different and more 

parsimonious interpretation of the crime 

switch data than that presented by Reiss 

(1980). 

2. Semi-Markov models 

for multiple victimization 

The basic idea suggested by Fienberg 

(1978) was the modelling of victimization 

for an individual or household as a point 

process p(t) >01, where Y(t) = j at 

time t if t e individual was last a victim of 

crime type j. A starting point for such 

modelling is the semi-Markov process with 

transition probabilities, 

Pt,(t) = Pr { Y(t) = jl Y(0) =i}, (1) 

where i and j run over the possible crime 

types under consideration, say 1 <i, j< r. 

(For details, see Cinlar 1975). 

These transition probabilities can be expressed directly in terms of two sets of 

quantities: 

(1) A matrix, M = {m, 

transition probabilities whic 

individual's "victimization propensities" 

given his current victimization state, i.e., 

his value of Y(t). 

(2) Ajamily of waiting time distributions, 9= { Gll(t), G12(t), ..., G~r(t) 

G21(t), ..., Grr(t)}, that characterize the, 

inter-victimization intervals (i.e., the times 

between victimizations) and which depend 

on the future victimization state as well as 

the current state of the Markov chain. 

of waiting times, 

the Markov chain. We also note that this 

modelling approach can be extended to 

handle more complicated processes involving m-step (for m > 2) transition probabilities in place of M, and corresponding 

wsiting time structures in place of 9or 

9. 

A useful way to think of this semi-Markov 

process is in terms of a sequence of random 

variables 

(XI, SI, X2, s2.\.. . ,Xn, Sn) (2) 

where n itself may be a random variable. 

The Xi's take values 1,2, ...,r, and they 

form a discrete-time, first-order Markov 

chain with transition matrix M, where 

' k-l k 

Y(t)=XkforC i=O St<t<2;SI. i-o (3)

The Sk's are positive random variables with 

for 1 < i Gr. 
Corresponding to the sequence of random 

variables in (2) is a vector of observed 

values 

and the likelihood of this vector given the 

model is 

whereJ(t) is the probability density function corresponding to the distribution 

function R(r). Here we have ignored xu, the 

unobserved victimization state at the time 

we begin to observe the process, and so, the 

corresponding inter-victimization interval 

which is observed only in a censored form. 

If n, the number of observed victimizations, 

is substantial, then the loss of information 

by ignoring the time lapse s8 (<so) from the 

beginning of the observation to the first 

recorded victimization is negligible. 

The important feature of the likelihood of 

expression in (6) is that it factors into two 

parts, the first involvifig the transition 

matrix M, and the second involving the 

can estimate the parameters of M sepamost individuals are fragmentary, with as 

' few as 20 percent of all sample members 

having complete 3-year records. The observed data are further complicated by 

several features of the NCS: 

(a) Time is discretized, i.e., measured by 

months. 

(b) Since victimizations are recorded 

only by month of occurrence, multiple victimizations within a given month are not 

sequenced in order of occurrence. 

(c) Series victimizations (see Fienberg 

1978 or Penick and Owens 1976 for a 

detailed discussion of this phenomenon) 

yield no information about individual 

inter-victimization times, only about their 

sum (at least within quarters of the year). 

(d) When both series and nonseries victimizations are reported during a given 

interval, the incidents cannot be ordered by 

time of occurrence. 

In the following section we briefly outline 

the approach adopted by Reiss (1980) for 

the handling of these problems to construct 

an observed crime-switch matrix in order 

to make inferences about the transition 

probabilities in the matrix M. 

3. Constructing a crime-switch 


matrix 


As Reiss (1 980) notes we can adopt any one 

The two tables reanalyzed in Section 4 are 

taken from Reiss (1980) and are based on 

household data for all households reporting two or more victimizations between 

Ji11ji i, 1972, and December 3i, 1975. Thus 

the data have been aggregated across 

households, and no attempt has been made 

to control for the size of the household or 

for any other household characteristics 

that might affect the transition probabilities. While this aggregation implicitly 

assumes a homogeneity of households so 

that the transition matrix M of Section 2 

does not depend at all on household characteristics, neither Reiss nor we in fact 

believe in such assumptions. Rather the 

aggregation of households has been done 

for the purposes of exploratory analysis 

and illustration. More refined analyses are 

not only possible, but also desirable. 

In constructing the crime-switch matrices 

used in Section 4, Reiss (1980) needed to 

handle many of the problems related to the 

recording of multiple victimizations discussed at the end of the last section. In particular he chose to record series victimizations as single incidents in the month of 

first re~orted occurrence. or at the beginning oia reference period if that month'iies 

outside it. Whenever multiple unordered 

incidents were recorded, the incidents were 

ordered using a randomization procedure. 

described by Reiss (1980). The randomization procedure clearly introduces considerably more symmetry into the data than 

we would expect to be present in the original unobserved victimization sequences. 

The symmetry in the constructed crimeswitch matrices is discussed in the course of 

our analyses. 

Finally, the data used by Reiss are based on 

rately from those underlying the {~(t)}. 

The first component of the likelihood can 

be rewritten as 

where n, is the number of transitions 

observed from victimization state i to 

of four choices regarding the unit at risk for 

our analysis of repeat victimization: 

(1) The household, using both personal 

victimizations for all household members 

and household victimizations. 

(2) The household, using only household victimizations. 

(3) The individual, using only personal 

victimizations. 

such transitions in the observed sequence, 

(5), we have that 

r r 

C 2 n,,= n - 1. 

Since M ={mi,} is". matrix of transition 

probabilities, we have that 

so that the likelihood function in (7) consists of a product of r multinomials. 

For each individual or household in the 

NCS we can, in principle, collect full information of the form (6) for a full 3-year 

period. Unfortunately, the data records for 

victimization state j. Since there are n - 1 (4) The individ'al, 'sing both ~ersonal both bounded and unbounded inteNiiws. victimizations and household victimizations. 

In Section 4 we analyze a crime-switch 

matrix constructed by Reiss for category 

(I), households with all victimizations. 

households used in the construction 

of the sample may be in the sample for from 

one to seven interviews, each of which yields 

victimization information for the preceding 

6-month period. Given the potential reporting biases associated with time in 

sample and differential dropout rates of 

various groups (see the discussion in Fienberg 1978), more refined analyses than 

those reported here should attempt to control for those factors in some way. 

4. Analyses of crime-switch data 

Our analyses here are carried out on two 

related tables of crime-switch or victimization transition data constructed, discussed, 

and analyzed previously by Reiss (1980). 

Table 1 gives the data classified by 20 detailed types of crime, and Table 2 gives an 

aggregated version of Table 1 using 8 major 

crime types. 
We begin with an analysis of the data in This corresponds to the model of quasi- some form of quasi-homogeneity holds for 

Table 1 and treat the counts as if they were symmetry, discussed in Chapter 8 of subsets of the cells in the table. Because of 

the {n,} of expression (7) in Section 2. Bishop, Fienberg, and Holland (1975), and the relatively large number of observed reWhat we would like to do is model the from Table 3 we see that this model pro- peat victimizations of the same type relamatrix of transition probabilities, M. The vides a remarkable fit to the data-G2 = tive to the expected values for the homoge- first question we ask is: Are the rows of the 174.9 and x2= 167.1, with 169 d.f. (We need neity model, the first quasi-homogeneity matrix M in fact the same, i.e., do we have to fit the model of quasi-symmetry rather model we explore is based on dropping the 

homogeneity of row proportions? The than the model of symmetry because of the diagonal cells and corresponds to the wellanswer to this question is clearly no, as can marginal constraints on the {m,,}.) This known mover-stayer model discussed in 

be seen from the values of the goodness-of- feature of symmetry in the observed data the context of social mobility studies. 

fit statistics reported in Table 3 for this was also noted by Reiss (1980) and partial- While this model gives a substantially immodel, GI = 12,420 and X* = 18,410 with ly anticipated earlier in this paper when we proved fit (GZ = 2261 and XZ = 2505 with 

361 d.f.1 discussed the use of randomization to 341 d.f.), it still does not fit the data well. 

Next we explore the question of symmetry order the unordered incidents. As a conse- Next, we used the 8 major groupings of 

of transition probabilities, i.e., quence of the excellent fit of the symmetry crime from Table 2 and dropped the corremodel of expression (lo), we treat cells 

above and below the main diagonal in a 

subject, of course, to the constraints, (9), symmetric manner in the followinganalyses. 

that the m, sum to 1 over j, i.e., Since the model of homogeneity of row 

proportions does not fit the data, it is 

= 1 for all i. natural to explore whether the model fits a 

restricted subset of the data, i.e., whether 

j 

'This value of x 2differs slightly from that reported by 

Reiss (1980). whocombines the categoriesfor rapeand 

attempted rape, and for purse-snatching and attempted 

purse-snatching, yielding an 18 18 table. Reiss 

reports X2 = 17,461 with 289 d.f. for this collapsed 

table. 

Table 1. 

Purse Type of crime Att. Serious Minor Att. Att. snatch, reported as Rape rape assault assault assault robbery pocket preceding incident picking 

Rape 6 3 8 1 5 2 2 1 

Attempted rape 1 16 6 9 21 I 6 2 

Serious assault 2 11 119 75 212 37 19 18 

Minor assault 4 8 83 152 244 22 20 21 

Attempted assault 11 29 199 228 1,685 59 81 37 

Robbery 2 4 50 30 89 27 23 

Attempted Robbery 1 5 30 21 762 27 54 12 

Purse snatchlpocket picking 1 2 21 19 47 26 9 46 

Attempted purse snatch 3 2 10 2 3 1 

Personal larceny, $50+ 7 15 110 99 401 61 44 44 

Personal larceny, under $50 16 33 238 292 1,314 126 1 36 144 

Attempted personal larceny 1 3 25 34 115 22 24 15 

Burglary, forced entry 7 17 90 59 199 42 25 27 

Burglary, no forcible entry 9 11 85 107 319 45 34 41 

Attempted burglary 8 46 46 166 30 15 23 

Household larceny, $5Ot 4 8 62 61 238 43 24 30 

Household larceny, under $50 7 18 89 154 554 7 5 49 64 

Attempted household larceny 1 4 11 8 74 4 11 3 

Motor vehicle theft 1 1 29 24 78 20 11 16 

Attempted motor vehicle theft 1 12 16 62 8 12 5 

Total number 81 197 1,316 1,437 5,892 741 606 573 

*Correspond to Table 2a in Reiss (1980). 

w 
sponding 8 diagonal blocks of cells.2 The 

resulting quasi-homegeneity model again is 

an improvement over the preceding model, 

but still does not fit the data well(G2= 1140' 

and X2 = !238 with 309 d.f.1. 

Rather than continue the analysis on Table 

1, we choose at this point to switch to Table 

2, which uses only the 8 major crime types. 

Again, for this reduced table the model of 

quasi-symmetry fits well (G2 = 24.4 and 

X? = 24.0 with 21 d.f.), while the model of 

homogeneity of row proportions fits 

poorly (G* = 8762 and X2 = 11,190 with 40 

d.f.). The quasi-homogeneity model based 

'on the table dropping the diagonals once 

again gives a remarkable improvement in 

fit, but still does not fit the data adequately 

(G2 = 383.9 and X2 = 404.3 with 41 d.f.). 

The 8 groupings involved rows and columns as follows: [1,21, [3.4,51,[6.71, [8.91, [10,11,121. [13,14,15]. 

[16.17,18], [19,20]. Since 4 diagonal blocks of 9 cells 

and 4 diagonal blocks of4 cells are dropped, there are 

361 - 4 x 9 - 4 x 9 = 309 d.f. for this model. 

We continue, dropping pairs of cells above 

and below the diagonal (i.e., (ij] and (j,i)), 

and fitting the model of quasi-homogeneity 

to those that remain. At each stage we drop 

the pair with the !argest standardized 

residuals and, if there is no clear choice, we 

.try a few likely candidates and take that 

pair which reduces the value of G2 the 

most. The resulting chi-square values and 

corresponding d.f. are reported in Table 4. 

Model (g) in Table 4, which is singled out 

by this procedure, fits the data reasonably 

well (G2 = 62.3 and X2 = 64.7 with 29 d.f.), 

especially when we recall that the symmetry is still not being handled directly by 

the modelling here. A closely related model 

with the same d.f., which actually fits the 

data better and is more easily interpretable, 

is given in the last line of Table 4. What it 

suggests is elevated occurrences above 

those expected from the quasi-homogeneity 

model for pairs of successive crimes involving personal violence (categories 1, 2, and 

3) as well as those involving theft without 

personal contact (categories 5, 6, and 7) 

plus elevated occurrences of the pairs of 

successive crimes involving purse-snatching 

and personal larceny. The reasonable fit of 

this model suggests that those patterns 

detectable in repeat victimization data are 

associated with crimes of similar type. This 

observation should lead to further investi-, 

gations regarding the vulnerability or 

"proneness" of certain groups of households to certain types of crime. 

We note in conclusion that those pairs of 

cells, singled out as departing from the 

quasi-homogeneity model in the preceding 

analysis, differ from those singled out by 

the techniques used by Reiss (1980), and 

the resulting model seems much easier to 

interpret. 

5. Suggestions for future 

analyses of longitudinal 

victimization records 

The semi-Markov model proposed in Section 2 leads to the separate analyses of data 

on victimization switches or transitions 

and of data on inter-victimization interval 

distributions. In Sections 3 and 4 we have 

suggested some analyses that can be usefully performed on the victimization switch 

data. 

Repeat victimization data for 20 crime categories: Reported crimes by households with two or more victimizations 

while in survey, July 1, 1972, to December 31, 1975 

Type of crime reported as following incident 

HouseAtt. Bur- Bur- H;;;- hold Att. MO:or Att. 

sonal gla~, glary, bur- motor Total 

purse larceny, larceny, Per- no larceny, house- sonal larceny, under hold vehicle number snatch $50+ larceny force force glary $50+ $50 larceny theft theft 
, 

Table 2. Repeat victimization data for eight major crime categories: Reported crimes by householdswith two or more victimizations 

while in survey July 1,1972, to December 31,1975 (adapted from Table 1) [Source: Reiss (1980) I 

2nd victimization Purse 

in pair/ ,st victimization Rape Assault Robbery Snatchingl pocket larceny brg!ary Hy::z'd $%: Totals 

in pair picking theft 

Rape 26 50 11 6 82 39 48 11 273 

Assault 

Robbery 65 2,997 238 85 2,553 1,083 1,349 216 

12 279 197 36 459 197 221 47 

8.586 

Purse snatching. 1,448 

pocket picking 3 102 40 67 243 115 101 38 703 

Personal larceny 75 2,628 413 229 12,137 2,658 3,689 687 22,516 Burglary 52 1,117' 191 102 2,649 3,210 1,973 301 9,595 Household larceny 42 1,251 206 117 3,757 1,962 4,646 391 12,372 Motor vehicle theft 3 221 51 24 678 301 367 269 1,914 

Totals 278 8,645 1,347 660 22,558 9,565 12,394 1,960 57,407 

These analyses of the first-order observed 

transition matrices represent only a first, 

and very exploratory step in the analysisof 

longitudinal victimization data from the 

NCS. In addition to disaggregating the 

data in the various ways suggested in Sections 3 and 4 and repeating similar analyses, we also need to address more carefully 

the procedures used to order the unordered 

victimizationincidents and to handleseries 

victimizations and how they related to the 

occurrences of other victimizations. 

We also need to begin analyzing intervictimization interval data and to concern 

ourselves with the overall usefulness and 

goodness-of-fit of the full semi-Markov 

model. 

Because of the peculiaritiesassociatedwith 

the data from the NCS (see Fienberg 1978), 

many of these more elaborateanalyseswill 

require new statistical methods or innovative adaptations of existing techniques. 

-

The author is indebted to Albert J. Reiss, Jr., 

who providedthe data analyzedinSection4and 

whose original analyses suggested those carried 

out in this paper. Thanksare also due to Dennis 

Jennings, who assisted with the computations 

and analyses. 

Table 3. The goodnessof-fit for various loglinear models applied to repeat victimization 

data of Table 1 

Likelihood ratio Pearson 

Model df. chi-square chi-square 

~2 ~2 

Homogeneity of row proportions 361 12,420 18,410 Quasi-symmetric 169 174.9 167.1 

Quasi-homogeneity

(a) dropping diagonal cells 341 2,261 2,505 

(b) plus blocks of cells for 8 

major crime groupings 309 1,140 1,238 

- . 

References 

Table 4. The goodnessof-fit for various loglinear modelsapplied to repeat victimization 

Data of Table 2 

Likelihood ratio Pearson 

Model d.f. chi-square chi-square 

~2 ~2 

Homogeneity of row proportions .49 8,762 11,190 Quasi-symmetry 21 24.4 24.0 

Quasi-homogeneity

(a) dropping diagonel cells 41 383.9 404.3 

(b) plus (6.7) pair 39 234.9 252.2 

(c) plus (2,3) pair 37 172.4 189.7 

(dl plus (3,4) pair 35 128.7 131.6 

(a) plus (1.2) pair 33 103.7 105.9 

(f) plus (2.7) peir 31 83.5 85.4 

(9) plus (2,8) pair 29 62.3 64.7 

Quasi-homogeneity

dropping diagonal cells plus 

(121, (1,3), (2,3), (3,4), (5,6), and (5,7) pairs 29 67.4 72.1 

Quasi-homogeneity

dropping diagonal cells plus 

(121, (1,3), (231, (3,4), (5.6) and (6,7) pairs 29 51.6 53.2 

Bishop, Y. M. M., S. E. Fienberg, and 

P. H. Holland (1975) 

Discrete multivariate ana!rpsis: Theory and 

practice. Cambridge, Mass.: M.I.T. Press. 

Cinlar, E. (1975) 

Introduction to stochastic processes. Englewood Cliffs, N.J.: Prentice-Hall. 

Fienberg, S. E. (1978) 

"Victimization and the National Crime Survey: Problems of design and analysis." In K. 

Namboodiri (ed.), Survey sampling and measurement, New York: Academic Press, pp. 89-106. 

(Reprinted in this volume.) 

Penick, B. K., and M. E. B. Owens (eds.) 

(1976) 

Surveyingcrime. Washington, D.C.: National 

Academy of Sciences. 

Reiss, A. J., Jr. (1980) 

"Victim proneness in recent victimization by 

type of crime." (In this volume.) 
Sentencing andparok 


Quantitative approaches 

to the study of parole 

RICHARDPERLINE 

Department of Psychology 

University of Chicago 

HOWARDWAINER 

Bureau of Social Science Research 

Washington. D.C. 

The first part of this paper,uses Federal The second part of this talk deals with 

parole data in an attempt to develop a parole data and their adequacy. In this secmodel for the parole system as it stands and tion we shall discuss data from individual 

to predict recidivism by treating it as a states gathered under the auspices of the 

latent trait. The second part discusses the Uniform Parole Reports project (hereafter 

adequacy of Uniform Parole Report referred to as "UPR Data''). We have re- 

(UPR) data for states. cently had the opportunity to do an evaluation of the UPR data for LEAA, and the 

appalling results have important implicaOmnia quae evenlura sun:, tions for those interested in doing parole in inrerro jaren:.' research. We shall keep federal data sepaTHE AREA OF PAROLE RESEARCH is rife rate from state data. This does not mean 

with dissension and disagreement, which that federal data are better than state data, 

appears to us to be entirely justifiable. We but only that we don't know about the reliwould like to add to the disagreements ability of the federal data. 

without further obscuring the vast darkness of the topic. This paper will be broken Establishing a quantitative model into two parts. The first part deals with for de facto incarceration rules 

some analyses we have done on Federal 

parole data. In this section we will try to Parole standards are set to indicate to the 

develop a model for the parole system as it parole board how long a particular kind of 

stands and to predict recidivism by treating convict should stay in prison. These are in 

it as a latent trait. For those who are in a the form of upper and lower bounds for 

hurry, our results are at least as good with each cell in a two-way categorization. The 

this approach as with any other, but still categorization reflects two schools of 

leave a great deal to be desired. thought on incarceration: 

'"Everything which is to come lies in uncertainty" 

(from preface to Raleigh's Hislory of :he World, 

1614). 

Table 1. 

Offender category 

1 2 3 4 

Offense severity 

category 

1 

2 

3 

8 

10 

11 

10 

14 

15 

12 

18 

19 

14 

22.5 

23.5 

4 14 18 22 26 

5 23.5 29.5 34 39 

(1) "Just dessertsp'-"you did something 

bad so youstay in-the badder the longer." 

(2) Rehabilitation-"you are more likely 

to recidivate than he is, so you stay in 

longer." 

These two schools of thought are concretized in the parole standards. The recommended bounds are a matrix in which 

the rows reflect the seriousness of the 

offense-the least serious at the top, the 

most serious at the bottom. Seriousness 

was determined through some sort of 

scaling, although how and by whom, I 

don't know. 

The columns of this matrix are determined 

by "Salient Factor scores,"in which a set of 

I1 variables are scored zero-one. The sum 

of the convict's scores on these variables 

yields his salient factor score, which is supposed to be related to the probability of 

recidivism (r* = 0.07). The federal guidelines collapse these salient factor scores 

'into four categories (0,1,2 = I; 3,4,5 = 11;6, 

7,8 = 111; 9, 10,ll = IV). The midpoints of 

the recommended sentence length intervals 

are shown inTable 1 by offender categories 

and by five seriousness of offense categories (in months for adults). 
I

"" '. 

Row Row effects I

1 2 3 4 medians (row median.-gr. md.) I I 

Grahd median 1.23 I 1 

Table 3. 

I -.I5 -.04 .04 .ll column medians = column effects 

The same multiplicative model (with difTable 4. ferent values.for the parameters) holds for 

juveniles as well. This model and its fit are Residual from model (in logs) shown in Table 6. 

We are then reasonably well assured that 

the existing parole policy corresponds

-.OI .02 closely to a multiplicative model in which 

.02 .1 


characteristics among adults, and about 

Our first interest was to identify the mode1 twice as much amOngjuveniles. 

underlying this structure. The sentence 

lengths were originally determined empirically as a measure of the de facto sentence 

structure for the majority of offenders. We 

analyzed these data using traditional twoway table decomposition methods. That is, 

inspection showed that an additive model 

was not appropriate (this is easily seen by 

fitting an additive model and seeing the 

substantial trends in the the residuals). We 

thus tried a multiplicative model by first 

calculating logs and taking out row medians; these correspond to seriousness effects 

(Bishop, Fienberg, Holland 1975; Tukey 

1977; Neithercutt, Moseley, Wenk 1975). 

We then calculated column medians of the 

residuals and subtracted them; these correspond to offender effects. The resulting 

matrix of residuals corresponds to the residuals from the model. As can be easily 

seen, these are all small. The effects were 

then transferred back to months and the 

total model specified. 

Table 5. 

Adults 

Offender effects 

.71 .89 1.10 1.35 19.95 


.2 .2 -. 1 -.8 .55 

-1.2 0.0 .7 1.2 .79 Offense 


-. 2 .2 .I .1 1 .OO seriousness 


-.3 .1 .7 .3 1.29 effects 


-1.4 -. 2 -. 3 -1.7 2.29 

Residuals (months) 


Residuals = Data Fit 


Fit = (19.95)x Offender eff. x Offense eff. 


Improvement? 

Having identified the de facto structure of 

parole policy, the road toward possible improvement is clear, and involves two steps: 

(1) Improve the accuracy of the estimates 

of seriousness of crimes, so that a more 

accurate classification is possible. 

(2) Improve the scaling of prisoner characteristics so that the prisoner effects more 

closely correspond to the likelihood of 

recidivism. 

Let us briefly look at step (1). Shown in 

Figure 1 and Figure 2 are plots of seriousness effects plotted against category. It is 

clear that categories 1-4 for both juveniles 

and adults are linearly related to incarceration length, but when crossing into category 

5 there is a major jump. It would seem that 

there is room for about4 intermediate categories between the crimes which correspond 

to category 4 and those in category 5. It 

would seem that finer discriminations are 

possible. Of course such fine discriminations are made as viewed by the increased 

width of allowable sentences for the more 

serious crimes. Why not make this explicit? 

We did not do the obvious scaling experiment, but the details of how to do such a 

study are clear (Torgerson 1958). Use classical scaling methodology with some 

Thurstonian model and have expert judges 

decide which of two paired crimes is the 

more serious. 

Step (2) was one which we found interesting. Could we improve upon the results 

that Hoffman and his colleagues (Hoffman 

and Beck 1974) had obtained through their 

use of multiple regression? They regressed 

a variety of variables against the binary 

variable (Recidivate-yes or no). We know 

very well that alternative models appear, at 

least on the surface, to be more suitable for 
test. We used a Rasch logistic model 

I
Table 6. 


Youth 

I Offender effects 1

.9 .8 .8 .7 .6

-. 7 .2 1.2 2.6 .9 Offense 

-.9 -.3 .3 1.4 1.2 seriousness 

-.3 -.4 -.4 -.5 1.2 effects 

.9 .4 -1.5 -. 3 1.9 

(Rasch 1960) to fit these data (n = about 

500) and looked at goodness-of-fit of the 

model. (We used differential slope models 

as well, but the fit wasn't increased and so 

we stuck with the equal slope model.) 

Associated with each variable is its "difficulty," here interpreted to mean how easy it 

is to have that variable scored I. Thus 

"planned living arrangement" is the 

Residuals (months) 


Fit -(17.0) x offender eff. x offense eff. 


Figure 1. 

Adult offenders 

Serlousness 1 75 


effect 1 50 


(~nmonths) 25 


1 00 

75 


50 


1 2 3 4 5 @0@@ 

Serlousness category 

A 


a binary criterion than linear regression. 

Also, it didn't seem that it would be that 

hard to improve on a method whose crossvalidated accuracy only accounted for 7 

percent of the variance. It should be noted 

that there is a severe restriction of range 

~roblem. in that we should give proper 

credit to'parole boards for knowing some- thing. hat is that they tend to keep in the 

really bad characters. The ones released are 

at the upper end of thedistribution and it is 

therefore harder to discriminate among 

them. At a guess, I would think that we 

psychometricians don't do all that much 

better; 1 don't know how much of the variFigure 2. 

Juvenile Offenders 

seriousness '" ' - .. 

,'*" Hypothetical 

effects 1 00 

.75 


.50 


12345678B 


Seriousness category 

I ance among Haward students is accounted 

for by SAT scores, but 1 imagine it isn't 

overwhelming. This same restriction of 

,range presumably exists in parole decision. 

Thus we must not be over-hasty in denigrating the 7 percent figure. 

Our approach was to think of the individual's background data as a test that he 

takes. There were eight variables that entered into this test which can be considered 

"predictor variables" and a single criterion 

variable "parole revoked." The eight variables are shown in Table 7. There is 

nothing magicai about the choice of the 

criterion var%ble;except that we chose it to 

be different from the other variables. We 

might just as well wish to predict one of the 

other variables, so we included "parole 

revoked" as one of the "items" and judged 

how well it is described by the rest of the 

"test" by looking at its r.b,, with the total 

fit 

"easiest" (86 percent had them) whereas 

"drug history" is the "hardest" (only about 

22 percent had one). Each person also had 

an "ability" score (perhaps "returnability" 

is a better term). The difference between a 

person's returnability and the difficulty of 

the item describes the likelihood of that 

person having that particular characteristic. To predict recidivism we calculated 

the probability of a person having the characteristic "recidivate." The r.h,, reflects the 

relationship between each "item" and the 

total test. Note that the r.h,, associated with 

recidivism = .57 (squared = .32). 

We can see from the results in Table 7 the 

general extent of fit, and those variables 

which seem to fit. Note that such variables 

as "planned living arrangement" don't 

seem to load too heavily on this trait. One 

could use such schemes to make decisions 

as to the importance of various kinds of information. The variables chosen and their 

scoring were taken precisely from the 

methodology Hoffman et al. developed. 

We were not given free access to all data, 

and so had to content ourselves to these. 

Thus these preliminary results look promising. Upon cross validation on a neutral 

sample there was some shrinkage. Our best 

guess as to the amount of variance accounted for on a neutral sample is between 

Table 7. 

Variable 

Prior conviction 

Age at first commitment 

Prior Incarcerations 

Parole revoked 

Verified employment 

Grade claimed 

Auto theft 

Drug history 

Planned living arrangement 

Difficulty Ann sq. '.his 

1.12 .61 .76 

-1.36 .63 .57 

-0.07 .65 .82 

-0.83 .74 .57 

-0.23 1.05 .41 

0.88 1.06 .38 

-1.18 1.07 .33 

-1.57 

2.20 

1.36 

1.73 

.20

.lo 
15 and 20 percent. A bit of an improvement, 

but nothing to write home about. 

A careful analysis of fit indicated that the 

model could be rejected, but what does it 

then mean to say that there is a single underlying dimension of "likelihood of recidivism?" We tried a variety of other schemes: 

the most interesting one was using Kruskal's monotone analysis, which showed 

that the best monotonic transformation to 

additivity did not fit much better than the 

Rasch model. We conclude from this that 

although the Rasch model doesn't fit, it 

does about as well as any single factor 

model. 

Parole data-UPR 

The preceding analyses were done on Federal parole data. There exists another data 

set, with longitudinal records running 3 

years on very large samples. These are the 

Uniform Parole Reports data. These data 

have been gathered by the National 

Council on Crime and Delinquency.2 

These data have been gathered for almost a 

2~ubstantialimprovements have been made in this 

program since this paper was prepared. For current 

information, write to Dr. James L Galvin, NCCD, 

760 Market Wt,Suite 433, SanFrancisco,California 

94102; telephone (415)956-5651. 

decade and contain a variety of useful information. After a careful examination of 

these data, I decided that the most valuable 

thing 1 could do with this forum would be 

to issue a short warning on the use of these 

data. Although these data have been declared "reliable enough" by their original 

gatherers (Neithercutt et al. 1975), our best 

guess is that they are not. A number of 

"shoe-box" reliability studies were carried 

out in which a very small number of cases 

were recoded, and the differences between 

their original coding and second coding 

were examined (n's in these were abdut 

160). The following results obtained: the 

percent agreement between the two codings 

for a seemingly foolproof variable like 

"ID#" was as low as 93 percent. This was 

called 'high"-I would call it embarrassing. 

The worst variable (in terms of reliability of 

coding) was "other prior sentences" which 

averaged about 53 percent but for some 

agencies was as low as 27 percent. Thus if 

one were using such a variable in any prediction scheme accuracy of prediction 

would certainly suffer. Overall accuracy 

was 80 percent which included such (relatively) failsafe variables like "is he dead?" 

One agency got "sex" wrong 4 percent of 

the time. 

There is great variability of accuracy across 

reporting agencies. Sadly, the reporting 

agencies are anonymous so you can't be 

sure how good your data are. These problems are being corrected, and we have reason to hope that in the future UPR data 

will be useful and reliable. We know for 

sure that the reporting agencies will no 

longer be anonymous. 

Refeences 

Bishop, Y., P. Holland, and S. Fienberg (1975) 

Discrete multivariate analysis. Cambridge,

Mass.: M.I.T. Press. 

Hoffman, P. B., and J. L. Beck (1974) 

"Parole decision-making: A salient factor 

score." Journal of Criminal Justice 2:195-206. 

Neithercutt, M. G., W. H. Moseley and 

E.A. Wenk (1975) 

Uniform Parole Reports: A notional correctional data system. Davis, Calif.: NCCD. 

Rasch, G. (1960) 

Bobabilistic models for some intelliaence and 

attainment tests. copenhagen: ~anrnarks Paedogodiske Institut. 

Torgerson, W. (1958) 

Theory and methods ofscaling. New York: 

Wiley. 

Tukey, J. W. (1977) 

Exploratory data analysis. Reading, Mass.: 

Addison-Wesley. 
Linear logistic msdeis ike parole 

decisionmaking problem 

KINLEYLARNTZ 

School of Statistics 

University of Minnesota 

This paper considers the use of quantitative DeGostin (1974), are given in Table 1. The 

aids in parole decisionmaking. Current guidelines for sentence length, also from 

practice employs a Burgess scale which Hoffman and DeGostin (1974), are given in 

weights items equally and ignores theinter- Table 2. For information on the developval (or ordinal) quality of the data. We pro- ment and recommended use of these guidepose logistic regression as an alternative lines, see Gottfredson, et al. (1974). 

statistical decisionmaking guide, and illustrate use of these techniques on data from Various states have also developed Salient 

the State of Minnesota. Also discussed are 	

Factor Scores that apply to their respective 

prison populations. The Federal set of nine the problems of selecting a few items from a items is not directly applicable because of pool of many items for construction of the the substantial differences in state and scale. Federal crimes. In Minnesota the Parole 

Decision-Making Project, headed by Dale 

1. Introduction 	 Parent, developed a Salient Factor Score 

A recent trend in parole decisionmaking 	 for aiding in state parole decisions; see 

Parent and Mulcrone (1978). Table 3 gives has been the use of objective scores, to be 	 the nine items found to be important in 'calculated for each potential parolee, 	 Minnesota. (In later implementation of the which attempt to estimate that individual's scale, three items were deleted: "juvenile chance of parole success. Specifically, a commitment," "had a sustained juvenile Federal Hearing Examiner is given a potential parolee's Salient Factor Score 

which, along with the type of crime, 

provides guidelines for sentence length. 

The Salient Factor Score is the sum of responses to nine items, seven of which are 

scored 0 or 1, and the other two are scored 

0, 1, or 2. The items for the Salient Factor 

Score, as reported by Hoffman and 

Table 1. Items in salient factor score 

ltem A 


No prior convictions (adult or juvenile) = 2 


One or two prior convictions = 1 


Three or more prior convictions = 0 


ltem B 


No prior incarcerations (adult or juvenile) = 2 


One or two prior incarcerations = 1 


Three or more prior incarcerations = 0 


ltem C 


Age at first commitment (adult or juvenile) 18 years or older = 1 


Otherwise = 0 


ltem D 


Commitment offense did not involve auto theft = 1 


Otherwise = 0 


ltem E 

Never had parole revoked or been committed for a new offense while on parole = 1 

Otherwise = 0 

ltem F 


No history of heroin, cocaine, or barbiturate dependence = 1 


Otherwise = 0 


ltern G 


Has completed 12th grade or received GED = 1 


Otherwise = 0 


ltem H 

Verified employment (or full-time school attendance) for a total of at least 6 

months during the last 2 years in the community = 1 

Otherwise = 0 

ltern I 


Release plan to live with spouse and/or children = 1 


Otherwise = 0 


petition," and "completed at least 10th 

grade.") The scale construction was based 

on the analysis of data collected on 93 1 out 

of about 1500 individuals released from 

Minnesota prisons in 1970 and 1971. The 

data set was divided into a construction 

group of 485 cases and a validation group 

of 446 cases. A number of regressions as 

well as Burgess scales were tried out before 

the final scale was selected. Note that the 

final Salient Factor Score was one of the 

best scales on both the construction and 

validation samples. Thus, in fact, all 931 

cases played a role in selection of the final 

nine items. 

In scale construction, each individual was 

classified as a "success" if, in the 2-year 

period following release, the individual was 

not convicted of a new felony. Low scores 

on the scale correspond to good prognosis; 

high scores to poor prognosis. Table 4 gives 

the group failure rates for the pooled construction and validation samples. Failure 

rates range from a low of 13 percent to a 

high of 54 percent. In Minnesota the Salient Factor Score is used, as in the Federal 

system, in conjunction with a measure of 

seriousness to aid in determining a release 

date. 
Table 2. Guidelines for decision-making: average total time served before relese 


(including jail time) -Adults _ 


Offender characteristics parole prognosis 


Severity of (Salient Factor Score) 


offense 


behavior Very good (3 9-9) Good (8-6) Fair (5-4) Poor (3-0) 


6-10 8-1 2 10-14 12-16 LOw months months months months 

8-1 2 12-16 16-20 20-25 Low moderate 	 months months months months 

12-16 16-20 20-24 24-30 Moderate 	 months months months months 

16-20 20-26 26-32 32-38 High 	 months months months months 

26-36 36-45 45-55 55-65 Very high 	 months months months months 

Greatest 	 (Greater than above-however, specific ranges are not given due 


to the limited number of cases and the extreme variations in 


severity possible within the category.) 


r 

Table 3. Final items for Minnesota Salient Factor Score 


' 
 -

Label -

Name 	 Category -

score 

Juvenile commitment YES 1 
 XI NO 0, 


Number of prior parole/probation failures 2 or more 1 x2 0.1 0 

Number of prior incarcerations 1 or more 1 

0 0 

Had a sustained juvenile petition YES 1 x3 	 NO 0 


Age at first adult conviction 19 or under 1
 x4 2OUP . 0 

x, Conviction previously-this offense 	 YES ? 


N0 0 


Completed at least 10th grade N0 1 


X6 YES 0 


This offense was burglary 	 YES 1 "7 N0 0 

X, 3 or more felony convictions 	 YES 1 

NO 0 ' 

Section 2 of this paper discusses a pubTable 4. Group failure rates lished reanalysis of the Federal data. Secfor Minnesota data base tion 3applies the same reanalysis technique 

Salient Factor Failure to the Minnesota data base. In Section 4an 

Score -rate alternative technique, logistic regression, is 

presented and applied to the Minnesota 0-1 	 13% 

2 - 3 17% data. Section 5 gives a simple validation of 

4 29% the various procedures, and the concluding 5-6 	 42% 

7-9 54 % 	 section gives the implications of this research for future studies. 

This paper presents a reanalysis of the 

Minnesota data base. The objective of the 2. Solomon's ~eanalySi8 

reanalysis is to explore logistic regression 01 the Federal data 

as a tool for predicting succ~ss.The Solomon (1976) reanalyzed the basic data data base split employed by the Minnesota set for 2497 prisoners used in construction Department of Corrections was also used of the Federal Salient Factor Score. He here, i.e., the same 485 construction cases showed that the nine items, used withequal and 446 validation cases. No new random 	 weights, could be reduced to four items, splits were tried. 	 provided unequal weighting was allowed. 

His final modkl showi decisively that the 

Salient Factor Score collapses groups that 

have.substantially different rates of risk. 

Solomon's final model was a logit model 

with four variables: 

PIJ~~ log -= w + Wl(,) + WZb)

1 - pykl 

(2.1) 

wherepiJk1 represents the true rate of failure 

for individuals in the cross-classification 

cell (i,j,k,l), and 

CWW) = 0, and 2 wzclj= 0. k L 

Table 5 gives the variables, categories, and 

weights for his final model. Using these 

weights we can calculate the estimated failure-rate for an individual with no priorconvictiork, no parole revocations, no auto 

theft, and planning to live with spouse as 

No prior convictions -0.6450 

No parole revocations -0.2344 

No auto theft -0.2210 

Plan to live with spouse -0.3852 

Constant 

Estimated failure rate = -

e-2,7s'' 

+ e1.75:1 

For additional reading on logit models, see 

Cox (1970) or Fienberg (1977). 

The important difference between Solomon's final logit scale and the nine-item 

Federal Salient Score is the weight 

assigned to each item. First, the logit model 

contains only four items. This has the effect 

of giving zero weight to the other five items. 

In addition, for the included variables, different weights were attached to each. In 

contrast, the Salient Factor Score assigns 

equal weights to each included item. Essentially, only the sign (positive or negative) of 

an item's estimated effect on failure rate is 

considered important. This method of 

forming a scale, based on equal weighting 

of items, is often referred to as the Burgess 

method. 

The main contribution of Solomon's study 

was to offer an alternative to the Burgess 

method for this decisionmaking problem. 

Previous studies had compared the Burgess 

method to linear regression analysis, and 

found the Burgess technique superiormainly on the grounds of robustness. However, the assumptions for linear regression 

are not usually met for this type of data. 

Solomon's proposal offers a statistical 

technique specifically tailored to the categorical nature of the data. 
- - 

- - - - - - - - 

- - - 

I 

Table 5. Weights for Solomon's final logit model 

Independent 

variables 

Number of prior convictions Dl: 

D, : Prior parole revocation 

D~: Auto theft 

D,: Plan to live with spouse and/or children 

Constant 

* 

Table 6. Weights and goodness-of-fit statistics for Minnesota logit models 

-

w I 

-0.6450 


+0.1054 


+0.5396 


+0.2344 


-0.2210 


+0.2210 


-0.3852 


+0.3852 


-1.2675 


dependent variable, also measured as zeroone, we can view the data in the form of a 

2 x 116 = 232 cell contingency table. For 

each cell, expected frequencies can be calculated based upon a particular logit 

model. The following two goodness-of-fit 

statistics compare the actual cell counts 

with the expected frequencies. 

(Observed -Expected)2 9

X2=c Expected (3.3) 

all 


cells 


Observed G2= 2x (~bserved)log(-).(3.4) all 


cells 


If the expected frequencies are large, it is 

reasonable to assess goodness-of-fit by 

comparing the calculated statistic with the 

percentage points of a chi-squared distribution with the appropriate degrees of freedom. However, here the expected cell frequencies are small., In such a case, the 

Pearson statistic X- has a level near the 

nominal rate, as long as the expected cell 

frequencies are not too small (Larntz 1978, 

Koehler and Qrntz 1980). The likelihood 

ratio statistic G- tends to be inflated if there 

are a large number of moderate (1 to 4) 

expected frequencies. 

Our situation involves large numbers of 

moderate and small expected frequencies: 

Thus by looking at the goodness-of-fit sta- . 

tistics listed in Table 6, we can see that 

Model V certainly does not provide an adequate fit, Models 11 and 111 are clearly 

describing the data well, and Models I and 

IV are borderline cases. It is intefesting to 

note that for the Burgess scale G' = 157.12 

(1 14 df). Degrees of freedom for the various models were calculated by considering 

the data as a 2 x 116 = 232 cell contingency 

table. Thus, Model V, which tests indel 

pendence in this table, has (2 - 1) x (1 16 - 1) 

= 115 degrees of freedom. Other degrees of 

freedom were calculated by subtracting 

one degree of freedom for each free parameter added to the corresponding model. 

The term ~4x7 was the only one of the 28 

possible interaction terms close to statistical significance at a standard level. To 

judge the statistical significance of the 

interaction, we look at differences in the 

G'-statistics for models fit with and without the interaction. In our case, 

Gif,,.,,,, i,i= GI?- G: = 13.41 

(1 df) 

or alternatively 

if,,.,^,^,,^ = GA - CAI = 	 14.17. 


(2 df) 


Categories 

0 


1-2 


3 or more 


No 


Yes 


No 


Y0s 


Yes 


No 


-

Model Model 


Variable I I I 


XI .68385 .66484 


xz .89731 .97447 
 x3 .23198 .26712 
 x4 .I3693 .71692 
 x5 .56074 .54484 
 xs .65332 .66840 
 x7 .45491 1.6642 
 xs .07271 .01055
 - -1 .SO50 x4x7 


CONST. -2.2979 -2.7047 


xa 132.31 120.09 

G~ 151.14 137.73 

df 107 106 

3. Logit models for Minnesota 

data set 

Following Solomon's example, logit models were fitted to the 485 cases of the Minnesota construction group. The variables 

used were those reported in Table 3 with the 

exception of "Number of Prior Incarcerations''-it was omitted because of a coding 

problem in our data base. Because of the 

zero-one nature of each of the X,'s, the logit 

model may alternatively be written as: 

wherep(x1, x2, . . . ,xg) represents the true 

rate of failure (felony conviction within 2 

years of release) for individuals with scores 

(XI, . . . , XX) on variables (XI, . . . , X8). 

There is a one-to-one correspondence between logit models written as in (3.1) and 

those written as (2.1). The estimated logits 

will be exactly the same irrespective of 

which form of the model is selected. Essentially, (3.1) is a regression analogue of the 

analysis of variance model (2.1). It is interesting to note that the Burgess scale (i.e., 

Salient Factor Score) says that ~(XI, x2, . . . ,xg) is merely a function of XI + x2 + . . . xs. 

Model Model Model 

-

Ill -

Iv -v 

- .78213 .82426 - 1.0480 1.0029 

.74209 


- .67259 .65932 -
 1.7314 .54767 


-1 .SO80 - -
 -2.5823 -2.1067 -.91196 


126.57 141.27 196.31 


141.21 155.38 225.50 


109 11 1 115 


Table 6 gives the estimated heights for several logit models. Model I is the logit model 

with all eight 'variables included, i.e.. 

p(x1, x2, . . . ,xg) does not depend upon 

(XI,. . . ,XX). Model IV excludes four of the 

variables which seem to have little importance in the construction sample. Models 11 

and I11 are different in that an interaction 

term was added to the basic Models I and 

IV, respectively. This is accomplished by 

merely adding a cross-product term to the 

model, e.g., for Model 111, 

p(x1, - . 7 ~8) log 1 -p(x1, . . . ,xa) 

To assess how well these models describe 

the 485 cases, goodness-of-fit statistics 

were calculated. For the eight independent 

variables there are 28 = 256 possible combinations; however, only 116 patterns 

actually appeared in the data. Adding the 
values of previously dichotomized varia- Table 9 gives the estimated regression 

Table 7. Weights for the burglary X 4. bles are now used. Also, sex has been added coefficients based on the construction 

( afirst conviction interaction -1 as a variable and juvenile record and edu- sample for five logistic regression models. 

Age at 1st cation have been deleted. Many more items Attempts at adding interactions did not 

adult conviction -Burglary were collected by the Parole Decision- prove fruitful in this case. The -2 log fvalue 

No Yes 

20 up 

19 down 

0.00 

0.74 

1.73 

0.67 

In both cases, the interaction is significant 

at 0.05 level, even after adjusting for the 

fact that all 28 possible two-factor interactipns were examined. Table 7 gives the. 

weights for the interaction cells. Note that 

"burglary" is not an important factor for 

"age at first adult conviction less than 20," 

but has a large effect for those "20 or over 

at first conviction." The risk of parole is 

greater for burglars first convicted at an 

older age. 

4. Logistic regression models 

The logit model with X's taking on 0 - 1 

values can be extended to permit continuous X variables or even a mixture of continuous and discrete variables (Nerlove and 

Press 1973, Fienberg 1977, Cox 1970). 

Table 8 lists the variables considered in this 

analysis. Note that a number of variables 

listed in Table 8 overlap with those in Table 

3. However, where possible, the actual 

Table 8. Variables for logistic regressions 

-

Label Description 

21 Number of parole/probation 

failures 

22 Number of incarcerations 

23 Age at first adult conviction 

Zq Number of felony convictions 

1 = Male 

Z5 Sex 2 = Female 

Z6 Age at release 

27 1 if offense was burglary, 

0 otherwise 

Making Project, but data were missing on 

many variables for a number of cases. 

(Three individuals were excluded altogether 

because of missing data. Although it was 

not done in this analysis, it should be noted 

that, assuming the omitted data were 

"missing at random," the missing values 

can be estimated via the EM algorithm 

(Dempster et al. 1977). Thus, all information in the full data set could be utilized in a 

complete analysis.) 

The logistic regression model describes the 

risk for individual i as 

log P= Po + PIZI+ prZ,r 1 -p, 

This model has exactly the same form as 

the logit model (3. I), but here we are allowing the independent variables (Z's) to take 

on any value, while in(3.1) the independent 

variables (X's) were constrained to be zero 

or one. Recent comparisons of logistic regression with linear regression have indicated that for certain uses, such as classification, logistic regression may possess certain advantages (Press and Wilson 1978). 

gives twice the log of the likelihood ratio 

assuming each of the 482 observations is 

Bernoulli with failure rate p, as in (4.1) (see 

Efron 1978). Again differences between 

likelihood ratio statistics can be used in 

comparing models; no overall goodnessof-fit test is possible here, however. From 

difference comparisons, Model 111 and 

Model 1V emerge as candidates for the best 

model. Model I11 needs only two variables 

for an assessment of an individual's risk, 

i.e., number of parole/probation failures 

and age at first conviction. Thus, an individual with one failure, first convicted at 

age 20, would have estimated logit 

A 

log -%I - P = 0.2803 1 + 0.22982(1) 

and estimated risk of a new felony conviction of fi = 0.263. Someone first convicted 

at age 18 with 7 prior failures would have 

estimated risk of 0.623. 

5. A simple validation 

of procedures 

A criticism that is often made of statistical 

model fitting is that although the final 

model fits the construction sample quite 

well, it does not do nearly so well when 

applied to new data. To avoid such criticism of their work, the Parole DecisionMaking Project divided the data into construction and validation groups. The final 

Salient Factor Score (see below, Figure 8 

and Table 11) did well on both groups. We 

now examine how well the logit and logistic 

regression models did when applied to the 

validation sample. 

Table 9. Regression coefficients for lpgikic regressions 

Variable 

21 

zz 

23 


24 

2s 

26 


27 

CONST. 

-2 log f 

df 

Note: 

Model Model Model Model Model 

-

I -

II -

Ill -

Iv -v 

.21955 .21645 .22982 .22061 - (2.81) (2.76) (3.17) (3.03) 

-.I1502 -.16966 - - -

(-.go) (-1.30) 


-.09425 -.lo352 -.00708 -.07426 - (-2.97) (-3.20) (-3.49) (-3.36) 


.09990 .09991 - - - (.96) (.95) 

-1.3631 -1.1829 - - - (-1.79) (-1.55) 


.00810 .01809 - - -
 (.41) (.88) - .61 760 - .6122 - (2.53) (2.59) 


0.4901 0.3586 0.28031 0.07633 -.91339 


525.7 519.4 531.6 525.1 577.3 


475 474 479 478 481 


Approximate t-statistics are in parentheses. 
Table 10. Results from applying Logit Model I in selecting 230 parolees 1 Table 11. Maximum D and average D 

LOWrisk 

High risk 

Total 

NOTE: PNF = gi = .583 pF = a = -344 

There are several possible techniques for 

checking the degree of validation for a predictive scale. One standard method is to 

separate the validation sample into several 

groups according to predicted risk and see 

whether the proportions of felons and nonfelons differ in the groups. Ideally, the low 

risk group would contain predominantly 

nonfelons, while the high risk group would 

contain predominantly felons. The statistical signifancance of the degree of separation of felons and nonfelons could be 

evaluated using a chi-squared test. It 

should be noted that this technique 

depends upon the nuhber of groups 

formed as well as the actual groupings. 

Different group formation could yield 

different degrees of validation when 

applied to the samc data. 

For comparisons in this.paper we have 

used the following method which has the 

advantages of (1) not depending upon any 

arbitrary grouping of the validation 

sample, (2) allowing direct comparisons 

between different predictive scales, whether 

or not the scales actually calculate an estimated risk (the method requires only an 

ordering of the risk), and (3) providing a 

natural graphical output illustrating the 

degree of validation. 

To illustrate the technique let us consider 

logit Model I. For each individual in the 

validation sample, calculate the estimated 

risk using the logit model weights given in 

Table 6. Order the individuals from low to 

high by this calculated risk. A good predictive scale would have a large proportion of 

the nonfelons in the "parole" group, while 

having a large proportion of the felons in 

the "nonparole" group. Now suppose, for 

example, that we were to "parole"230 indiFelon -

Total

43 230 


-

82 216 

125 446 

viduals. Table 10 summarizes logit Model 

1's performance in "parolingn 230 individuals. Of the 230 lowest risk scores 187 belonged to nonfelons. To measure how well 

the predictive scale separates the felon and 

nonfelon groups calculate the difference of 

the proportion of nonfelons assigned to the 

low risk group minus the proportion of 

felons assigned to the low riskgroup. In the 

example, 

and 

D = 0.583 - 0.344 = 0.239. 

Note the proportion "paroled" in this 

sample was fixed at 

Now consider calculating D for each possible "paroling strategy," i.e., for paroling 

1,2,3, . . . ,445 individuals, or equivalently 

forplol = 1/446,2/446,3/446,. . . ,4451446. 

Figure 1 gives a graph of D vs.plo~ for logit 

Modell. The higher D is for a given value 

of pltn, the better the predictive scale in 

separating nonfelons from felons. In 

Figure 1, the peak value of D is 0.2480. An 

"ideal scale" would have a peak value of D 

of 1.000. 

Figures 1-9 present graphs of Dvs.pror for 

4 logit models, the patterns for all figures 

are the same, although the peak values of D 

occur at different values of pr~. Table 11 

gives the peak values of D and also the 

average values of D (this corresponds to 

the area under the curve) for the nine 

scales. Logistic Model I11 hss the largest D 

value, while the Corrections Department 

scale has the largest mean. 

We now examine the individual figures 

more closely. First, logit Model I (Figure 1) 

and logit Model IV (Figure 4) are virtually 

identical, except for the noise caused by the 

four extra variables included in logit 

-

Model 

Logit I 


Logit II 


Logit I II 


Logit IV 


Burgess 


Logistic 1 


Logistic I I 


Logistic I I I 


Logistic IV 


Model 1. The same is true for logit Models 

I1 (Figure 2) and 111 (Figure 3). Thus, as 

expected, there is no gain in adding nonsignificant variables to the logit model. 

Similarly, although the interaction term is 

statistically significant, when we compare 

Figure 1 with Figure 2 and Figure 3 with 

Figure 4, the validation curves indicate that 

inclusion of the interaction term is helpful 

for some values of pr~l(0.2,0.4) while not 

helpful for others (p1o.1 = 0.4,0.6). The Burgess scale curve (Figure 5) is comparable to 

the logit models and perhaps even a little 

higher, but it must be kept in mind that its 

nine items were selected on the basis of the 

same construction and validation samples 

being used here, i.e., the full data. 

The logistic models (Figures 6-9) are 

clearly better when fewer variables are 

included, i.e., logistic Models 111 and IV. 

Logistic Model 111 (the two-variable 

equation) is particularly strong for p101= 0.6, yielding the highest D value for any 

validation. However, it does not do as well 

as other models for p101near 0 or 1. This 

may be unimportant sincep101 near 0 or 1 

imply strategies of paroling few or nearly 

all eligible prisoners. 

Although not improving greatly over the 

Burgess scale, the better logit and logistic 

models do perform well on the validation' 

sample. The two-variable logistic model 

did particularly well, especially considering 

that these two variables were selected from 

a pool of only seven items. The nine items 

in the Burgess scale were selected from a 

much larger pool, and since the same items 

were used in the logit models, the logit 

models' performances on the validation 

sample should not be surprising. In both 

logit and logistic cases, restricting the 

model to include only "significant" variables improved the validation performance. 
6. Discussion 

Figure 1. One aspect of the logit and logistic models Validation - Logit I that has been ignored in the compari- D 0.3- sons is the actual estimated risk value. 

Does this estimated risk have a frequency 

0 2. interpretation? To answer this question, we 

conducted a sampling experiment. Using 

0.1. 	 the 9,'s of the validation sample, Bernoulli 

random variables were generated to randomly assign an individual as a felon or 0.0 - nonfelon with probability j,or 1 -j,,respectively.1 Figures 10, 11, and 12 give - 0 1 - I 1 ' I 3 I ' plots of D vs. plol for the Monte Carlo 

00 	 0.2 04 06 08 10 runs on logit Model 1, logit Model IV, and 

P TOT logistic Model 111. If the j,'s are good I quantitative estimates of risk, the Monte 

Carlo curves should look the same as the 

original validation plots. The general 

Figure 2. shapes in all three cases are fine, but the 

Validation - Logit II values of Dm,, as given in Table 12 are 

shifted for both logit models. This is undoubtedly due to the greater degree of 

selection for the items comprising the logit 

scales-and thus also for the Burgess scale 

items. Note that the logistic Model 111 

curve and Dm,, are quite similar to those 

seen in Figure 8. Thus, when a great deal of 

selection occurs as in the Burgess scale 

constructio~, the usual construction-validation splitting is not enough. Double 

-01- . , 1 , , , , , , cross-validation (Mosteller and Tukey 00 02 04 06 08 10 1977) consisting of using separate samples PTOT 	 for (1) choosing items, (2) estimating coefficients, and (3) testing the scale likely 

would have reduced the overall effects of 

selection. 

Figure 3. 

Validation - Logit Ill The practical implications of thedata analysis results reported here are (I) to question 

the efficiency of the construction-validation 

splitting as currently practiced and (2) to 

offer a technique, logistic regression, 

whose assumption requirements are more 

in keeping with the data as collected. Related to the first point, we recommend use 

of double cross-validation when data are 

plentiful, and consideration of jackknifing 

techniques (Mosteller and Tukey 1977) 

-0.1 , , . , , , . , , when more must be squeezed from limited 

00 02 04 06 08 10 data. For the logistic regression versus PTOT" Burgess scale question, only experience 

with both will decide which, if either, is 

better. We recommend their joint consideration in any future projects, and certainly Figure 4. feel that logistic regression will prove to be 

Validation - Logit lV a better competitor than linear regression 

has been in the past. 

3 


'Computations were performed using FORTRAN programs on a CDC 6400 computer. Bernoulli random 

variables were generated from uniform random numbers by classifying the uniforms into one of two categories using the boundaries (O,lj,,I). The uniform random numbers were produced by a multiplicative congruential generator using modulus 2" and multiplier 5". 

Figure 5. 


Validation - Burgess Scale 


Figure 7. 


Validation - Logistic II 


D 03 

0 2-

0 1-

0 0 


-01- . , , , , , , , , 


00 02 04 06 08 10 

TOT 

-01 , , , , , , , , a 

00 02 04 06 08 10 

PTOT 

i 
References 

Figure 8. 

Validation - Logistic Ill 

0 03 

0 2- 

0 1 -

0.0 -

-01 n , n , 8 , 7 , . 

00 02 04 06 08 10 

PTOT 

4 


Figure 9. 

Validation - Logistic IV 

003 

-0 1 , , . , . , . , , 00 02 04 06 08 10 

PTOT 

Acknowledgments 

This research project grew out of material on the 

Federal Parole Project presented at the Workshop on Criminal Justice Statistics, held in 

Washington, D.C., July 1975. The workshop 

was sponsored by the Social Science Research 

Council Center for Coordination of Research on 

Social Indicators and the Law Enforcement 

Assistance Administration. The sponsors also 

provided additional financial assistance for this 

project. 1 am grateful to Sanford Weisberg, 

Ronald Christensen, and Sharon Yang for collaborative efforts in the early stages of this research. In addition, Stephen E. Fienberg provided valuable detailed comments on both the 

research and its presentation. The University of 

Minnesota Computer Center provided a grant 

for computing costs. Special thanksare owed to 

Dale Parent, Minnesota Department of Corrections, who provided the raw data and was particularly helpful in clarifying the coding procedures. 

Cox, D. R. (1970) 

The analysis of binary data. London: 

Methuen. 

Dempster, A. P., N. M. Laird, and 

D. B. Rubin (1977) 

"Maximum likelihood from incomplete data 

via the EM algorithm." Journal of the Royal 

Staristical Society 39: 1-38. 

Efron, B. (1978) 

"Regression and ANOVA with zero-one data: 

Measures of residual variation." Journal of the 

American Statistical Associarion 73: 113-121. 

Fienberg, S. E. (1977) 

The analysis of cross-classfled categorical 

data. Cambridge, Mass.: M.I.T. Press. 

Gottfredson, D. M., C. A. Cosgrove, 

L. T. Wilkins, J. Wallenstein, and 

C. Rauh (1978) 

Classijicarion for parole decision policy. 

Washington, D.C.: U.S. Government Printing 

Off ice. 

Gottfredson, D. M., L. T. Wilkins, 

P. B. Hoffman, and S. M. Singer (1974) 

The utilization of experience in parole 

decision-making Summary report. Washington, D.C.: U.S. Government Printing Office. 

Hoffman, P. B., and L. K. De Gostin (1974) 

"Parole decision-making: Structuring discretion." Federal Probation (December). 

Koehler, K. J., and K. Larntz (1980) 

"An empirical investigation of goodness-of-fit 

statistics for sparse multinomials." Journal of 

the American Statistical Association 75:336-

344. 

Larntz, K. (1978) 

"Small-sample comparisons of exact levels for 

chi-squared goodness+f-fit statistics." Journal 

of the American Statistical Association 

73:253-263. 

Mosteller, F., and J. W. Tukey (1977) 

Data analysis and regression. Reading, Mass.: 

Addison-Wesley. 

Nerlove, M., and S. J. Press (1973) 

"Univariate and multivariate log-linear and 

logistic models." Technical Report R-1306-ECA/ 

NIH, Rand Corporation, Santa Monica, Calif. 

Parent, C. G., and T. G. Mulcrone (1978) 

"The development and operation of parole 

decisionmaking guidelines in Minnesota." In 

D. M. Gottfredson, C. A. Cosgrove, L. T. Wilkins, J. Wallenstein, and C. Rauh, Class~pcation 

for parole decision policy, Washington, D.C.: 

U.S. Government Printing Office. 

Press, S. J. and S. Wilson (1978) 

"Choosing between logistic regression and 

discriminant analysis." Journal of the American 

Staristical Association 73:699-705. 

Solomon, H. (1976) 

"Parole outcome: A multidimensional contingency table analysis." Journal of Research in 

Crime and Delinquency (July) 107-126. 

Figure 10. 

Monte Carlo - Logit I 

00 0.2 04 0.6 0.8 1.0 

PTOT 

Figure 11. 

Monte Carlo - Logit IV 

D 04j 

0.31 

02-

01: 

0.0 -

-0.1 , , . , . , . , , 

0 0 0.2 0.4 0.6 0.8 1.0 

TOT 

& 

Figure 12. 

Monte Carlo - Logistic Ill 

-0.1, 9 , - , a , . , . 0.0 02 04 06 0.8 10 

PTOT 

Table 12. Maximum D for Monte Carlo 

samples from three predictive scales 

Monte Carlo Validation 

-

Model -Dmax 

Logit I .3885 .2480 

Logit IV .4072 .2729 

Logistic 1 11 .3075 .2844 
The effects of plea bargaining 

on the disposition of person and property 

crimes: A research note 

DAVIDW. BRITT 

Criminal Justice Program 

Nova University 

KINLEYIARNTZ 

Department of Applied Statistics 

University of Minnesota 

Many of the studies which have examined common experience-let alone the alterna- the various points in the process and if the 

the impact of offender and offense charac- tive paradigms for viewing the operation of outcomes at one stage had no independent teristics on sentence severity have been mis- the criminal justice system. For example, a bearing on the operation of these factors at 

specified because they have ignored (or recent analysis of the construction of judi- a later stage. Unfortunately, such assump- tried to hold constant) events such as pre- cia1 decisions has observed that for a tions appear to be invalid. Consequently, trial plea bargaining which took placeat an sample of judges having flexible attitudes many of the studies which have examined 

earlier stage in the process but which have a toward law and order, blacks and those the impact of offender and offense characcritical bearing on the outcome of sentenc- with larger numbers of current charges teristics on sentence severity have been 

ing decisions. Our approach to the analysis were more likely to receive short sentences misspecified because they have ignored (or of these phenomena is similar to the than whites and those with smaller num- tried to hold constant) events, such as pre- exploratory study by Burke and Turk bers of current charges (Hagen 1975:379). trial plea bargaining, which took place at 

(1975)in that we are considering a sample Such results are at odds both with an earlier stage in the process but which 

of all post-arrest dispositions. Our study conceptions of the criminal justice system have a critical bearing on the outcome of 

differs from theirs in that we attempt to which stress a bias against the dis- sentencing decisions. 

include the impact of plea bargaining on advantaged andconceptions whichemphasubsequent sentencing decisions. size offense characteristics. ~t is apparent A thorough review of the entire 

that models of post-arrest disposition have justice process as it isaffected by characteromitted variables which are crucial to an istics of the offender, the offense, and 

THE TESTING OF WHAT PASSES for understanding of the dynamics of the dis- in the structureat different points 

conventional wisdom often leads to position process, and it is these specifics- is beyond the of this paper. Suffice it 

conclusions which are apparently para- tion errors which have resulted in some of that the works On sentence 

doxical. Such is the case for recent the paradoxical results observed in recent length tHagen 1975; Burke and Turk 1975; 

attempts to structure and analyze the bias studies. Tiffany et al. 1975, for example) have been 

in criminal justice systems. As Burke and unable to come up with plausible interpreTurk (1975:313) have Faced with the problem of disentangling tations for what appear to be bizarre 

the the serial processes which un&rlie the conventional wisdom of criminology has processing of ''criminals" within the patterns in the operation of offender 

held that the socially disadvantaged are characteristics (race, sex, age, prior convicmore likely than the advantaged to be criminal justice System, n~uch current tions), characteristics of the offense (sever-' 

engaged by the criminal justice system, to research has sought to simplify the task by ity of offense, number of current charges) 

be prosecuted, tried, convicted, and to examining discrete aspects of this Process and system characteristics (type of counsel, 

suffer more severe upon convic- as a first step in the ultimate integration of bench vs. jury trial). What is missing from 

tion. Yet the findings of empirical analyses these separate analyses. Such an attack on all of these studies is some notion of the 

have been both ambiguous and occasion- the problem would be reasonable if the operation of pre-trial plea bargaining on 

ally at odds with the received wisdom of Same set of factors affected dispositions at the outcome of the sentencing decision. 

Some of thesestudies (Hagen 1975; Tiffany 

et al. 1975) have sought to minimize the 

Table 1. Results of testing the hypothesis that the variable is independent of incarceration influence of pre-trial factors by limiting the 

given seriousness and type of crime. sample of cases processed by the system to 

those above a minimum level of seriousness 

Variable -df -

G~ -

x2 -

T~ P-value(xz) which have reached trial. Since fewer than 

Sex 6 13.31 9.23 11.66 .25> p>.10 10 percent of the initial cases reach trial in 

Race 8 8.65 7.40 7.56 p>.25 most jurisdictions (Blumberg 1967; HeisPlea 15 30.58 24.48 27.01 .lo> p>.05 mann 1975), and since cases which reach 

Charge 10 25.03 20.38 21.81 .05> p>.025 trial are biased in that they have rejected 

No. initial charges , 7 2.61 2.70 2.66 p>.25 the plea-bargaining alternative (Tiffany et 

No. convicted charges 6 6.96 4.77 5.82 p>.25 al. 1975), this would seem to be an unacNO. previous arrests 9 32.23 28.31 29.31 p<.005 ceptable way of controlling the influence of 

Felony convictions 10 41.08 35.43 41.88 p<.005 pre-trial factors. 

Employment status 8 8.22 7.69 7.28 p> .25 Our approach to the analysis of these phe- Resisting arrest 8 12.44 10.99 10.80 .25> p>.IO nomena is similar to the exploratory study Weapon usage 7 10.84 8.32 9.03 p>.25 by Burke and Turk (1975) in that we are 
1 Table 2. 138 Criminal sentences classified by type of crime, seriousness of charge plea, change in charge, previous record 

and incarceration 

Good Fair Poor 

Previous record previous record previous record 


Type of crime, 


seriousness and 

change Plea No jail Jail No jail Jail No jail Jail 

Person, 

no change 

Guilty 

Nolo contendere 

1 3 

2 

2 

2 

5 

0 

of charge Not guilty 0 0 0 

Person, Guilty 

charge Nolo contendere 

changed Not guilty 

Property, Guilty 

low seriousness, Nolo contendere 

No change of charge Not guilty 

Property, Guilty 

low seriousness, Nolo contendere 

charge changed Not guilty 

Property, Guilty 

moderate seriousness, Nolo contendere 

no change of charge Not guilty 

Property, Guilty 

moderate seriousness, Nolo contendere 

charge changed Not guilty 

Propeny, Guilty 

serious crime, Nolo contendere 

no change of charge Not guilty 

Property, Guilty 

serious crime, Nolo contendere 

charge changed Not guilty 

Property. Guilty 

very serious crime, Nolo contendere 

no change of charge Not guilty 

Property, Guilty 0 2 

very serious crime, Nolo contendere 1 

charge changed Not guilty 0 

considering a sample of all post-arrest dis- charge the same as the initial charge or was Analysis and results 

positions. Our study differs from theirs in there some reduction in charge? 

that we are attempting to include the (6) Number of initial charges. With the number of variables that we 

impact of plea bargaining on subsequent (7) Number of convicted charges. deemed important to consider and the relasentencing decisions. (8) Number of previous arrests: Low (0, tively small sample size, we opted to make 

1, 2) or high (3 or more). an initial pass through the data toselect the 

(9) Number of adult.felony convictions: most important factors. Our review of the 

Data literature showed that seriousness of 

Two hundred sample cases were selected 

Low (0) or high (1 or more). charge and type of crime were both impor- (10) Employment status: Was the indi- tant factors in explaining the number of from the Denver, Colorado, courts under vidual employed or unemployed at the time individuals jailed. To decide which of the the auspices of State Courts Sentencing of the offense? 

Project. Sixty-two of these cases were (I 1) Type of crime: (a) Against propother variables to include, each variable 

eliminated from this sample: 5 because of erty, (b) against person but at most slight was tested to see if the hypothesis of condiinadequate data and 57 because of their injury, or (c) against person with serious tional (given seriousness and type of crime) 

being so-called "victimless" crimes. The independence between the variables and 

remaining 138 cases were analyzed to 

injury. incarceration was plausible. The chi-' (12) Resisting arrest: Did the individual square statistics and p-values for these tests determine the major factors used by judges resist arrest? 

in reaching the decision of whether or not (13) Weapon usage: Did the crime are given in Table 1. The four variables 

to incarcerate an individual convicted of a involve use of a weapon? yielding the lowest p-values were selected 

criminal offense. Thirteen variables were for further analysis. 

initially considered as possible factors: The dependent variable was incarceration, In the initial data analysis it became clear 

(1) Sex. i.e., whether or not the individual was sent that sentences for crimes against property (2) Race: White, other. to jail by the judge. had a different structure compared to sen- 

(3) Plea: Guilty, nolo contendere, or not tences for crimes against persons. To deal 

guilty. with this structural dissimilarity, the anal- 

(4) Seriousness of charge: Low, moder- ysis was split into two parts: crimes against 

ate, serious,or very serious. property and crimes against persons. Table 

(5) Change in charge: 1s the convicted 2 gives the data as used in the final analysis. 
-- 

-- 

I Table 3. Results of logit mow fittings for crimes against property 

1 Variables included in modal df G2 X2 TZ I 

Previous record, plea, charge seriousness 30 23.00 21.49 17.79 

Previous record, plea, charge 

Previous record, plea, seriousness 

Previous record, charge, seriousness 

Plea, charge, seriousness 

Previous record, plea 

Previous record, charge 

Previous record, seriousness 

Plea, charge 

Plea, seriousness 

Charge, seriousness 

Previous record 

Plea 

Charge

Seriousness 

None 

*x2 = C (Obs - EX^)' /Exp 

33 29.79 22.97 23.91 

31 23.14 21.56 18.09 

32 23.02 21.57 17.75 

32 57.59 49.33 46.21 

34 31.11 24.21 25.35 

35 29.94 23.17 24.03 

33 23.20 21.56 18.11 

35 67.1 1 57.24 54.73 

33 57.59 49.28 46.25 

34 63.00 51.19 52.23 

36 31.12 24.22 25.35 

36 68.07 57.14 55.97 

37 70.74 55.28 59.60 

35 63.61 51.73 53.06 

38 73.40 56.59 62.89 

T' = C (JUE+JVDS + 1- J4 txp + n2

G2 = 2 C Obs loge (Obs/Exp) 

When cell expectations are small, as they are in our examples, we examine all three chisquare statistics to evaluate the model fit (Larntz, 1975). 

I Table 4. Results of logit model fitting for crimes against persons 

I Variables included In model 

Previous record, charge, plea 

Previous record and charge Previous record, and plea , 

Charge and plea 

Previous record only 

Charge only 

Plea only 

None 

Record x plea + charge 

Record x charge + plea 

Charge x plea + record 

Charge x plea only -

*See footnote for Table 3 

Note tnat crlmes against ~ersons were not 

classified by seriousness: this was because 

almost all of these crimes were classified as 

serious offenses. Also number of previous 

arrests and felony convictions were combined into a new variable, previous record. 

A "poor" previous record meant the individual had one or more adult felony 

convictions. A "fair" record resulted from 

at least three previous arrests but no felony 

convictions. An individual had a "good" 

record if there were at most two recorded 

arrests with no adult felony convictions. 

The procedure for analyzing the data in 

Table 2 was to find the logit variant (Dyke 

and Patterson 1952, Goodman 1970) of the 

loglinear model (Bishop, Fienberg, and 

Holland 1975; Haberman 1974) that provided the closest fit to the data. 

Table 3 presents the results for the models 

fit the property crime sentences*and Table 4 similarly presents the results for the 

person crime sentences. BY examining the 

significance of the overall goodness-of-fit 

chi-sauares as well as the differences between' the chi-square statistics when one 

model is a submodel of the other, inferences may be drawn as to the major factors 

influencing the incarceration decision. 

For crimes against property, the logit 

model including only seriousness of'charge 

df G2 X2 T2 1 

7 13.82 

9 19.90 

8 18.41 

9 13.96 

10 24.54 

11 20.84 

10 18.47 

12 25.13 

3 12.15 

5 10.17 

6 12.77 

8 12.90 

I 


and previous record-with the latter playing a more important role-provides an 

adequate fit to the data. Table 5 gives the 

estimated percentage incarcerated based 

on these two variables. Those with poor 

records who have been convicted of a very 

serious crime have roughly a 95 percent 

chance of being incarcerated. The impact 

of previous record on incarceration' 

chances may be better appreciated by 

examining two other cells in Table 5. Even 

if the seriousness of the present crime was 

quite low, if the prior record of the convicted defendant was poor, he/she had 

almost a 60 percent chance of going to jail. 

But if the prior record of thedefendant was 

good, he/she had only negligible chance of 

going to jail no matter how serious the 

present crime. 

For crimes against persons, where almost all crimes were categorized as being 

serious, the logit model also includes just two variables: change and Table 

the estimated incarceration rates for 

crimes. 

Of those who either chose or were not 

allowed to enter into plea bargaining (at 

least with respect to an exchange of charge 

reduction for a plea of guilty), those who 

pleaded guilty had the highest chance of 

going to jail (78 percent). Those who were 

able to plead nolo contendere had only a39 

percent chance of going to jail. Pleading 

guilty was associated with a 50 percent 

chance of going to jail. These figures are 

dramatically altered by the apparent 

exchange of plea for charge reduction. For 

those who plead guilty with a reduced 

charge, the chances of being incarcerated 

drop from 78 percent to 48 percent. A similar drop in incarceration chances is noted 

for those pleading nolo contendere: from 

39 percent to 14 percent.' 

Discussion and conclusions 

Dispositions of crimes against property 

appear to be related to variation in the seriousness of the crime and the offender's previous record in a relatively straightforward 

way. As the crime becomes more serious 

and the offender's previous record becomes 

poorer, the chances of the individual's 

being incarcerated increase. Interestingly, 

as long as the previous record of the individual has not involved more than two 

arrests and no adult felonv convictions. 

there seems to be a bias against sending thd 

individual to iail-no matter how serious 

the present droperty crime is. Once the 

individual has been arrested more than 

twice previously, or has had a previous 

felony conviction, his chances of being 

incarcerated for the present offense escalate rapidly. But this appears to be the only 

bias in the property-crime dispositions, for 

neither characteristics of the offender (sex, 

race, employment status) nor his pleas or 

charge reductions appear to directly affect 

the decisionmaking process. 

These results for property crimes overlap 

substantially with those of Burkeand Turk 

(1975:326), who noted that the effect of 

previous incarceration on disposition 

severity remained important even after 

controlling for the nature of the offense.* 

They argued that such a pattern increased 

the tenability of an explanation based on 

ex-convicts' "vulnerability to the biases of 

legal control agents" and initiated an 

argument based on the presumed greater 

"propensity of ex-convicts for relatively 

serious crimes." In other words, even 

though there may be an association 

between prior record and offense seri- 

'We should note here that the length of sentence has not 

been taken into consideration. Hence, while these data 

suggest a rational strategy of pledging nolocontendere 

or of guilty if the plea bargainingoption is unavailable, 

a different pattern might have emerged had we been 

able to take length of sentence into account. 

?Burke and Turk (1975) found that agealso directly affected the dispositional process, although the impact 

of age was complica~ed and not amenable to 

nonspecu~ative. plausible explanation. 
-


Table 5. Estimated percentage incarcerated for crimes against property 

Seriousness of charge 

Low Moderate Serious Very serious 

Good O (12) (13) O (5) O (1) Prior 

i record 	 Fair 21 (9) 27 (3) 48 (6) 82 (5) 

Poor 58 (7) 66 (15) 83 (5) 96 (3) 

Note: Estimated percentages are calculated from logit model: 


P..
 log L=p+ai +p. 1-p..11 1 


where P.. is the probability of incarceration. 
 #I 

ousness, each makes a contribution to the 

reconstruction of the observed distribution 

of incarceration rates. 

Our results speak to the possibility of a 

threshold of vulnerability to bias on the 

part of legal control agents. Some degree of 

"criminality credit" appears to be granted 

to individuals who have had "good" prior 

records, so that individuals appear to be 

buffered from jail sentences until their contact with the machinery of the state has 

been relatively frequent or serious. If these 

results have any validity, one implication is 

that socially disadvantaged individuals are 

not being directly discriminated against at 

this point in the dispositional process. It is 

quite possible, of course, that variation in 

both the seriousness of crimes and 

poorness of records could be traced to both 

race and occupational status (Burke and 

Turk 1975). It is also possible that more 

complicated interactions of race and age 

might affect the propensity to commit 

serious offenses (Black and Reiss 1970) 

and/or the poorness of prior record. But in 

our admittedly small sample (as well as in 

that of Burke and Turk), blacks do not 

appear to be diyferentially vulnerable to 

being labelled as a "repeat offender," or 

"career criminal." Were this the case, we 

should have at least observed an interaction of race and prior record in the disposition process. 

A somewhat different picture emerges 

regarding the structuring of disposition~of 

crimes against persons. To recapitulate, 

charges were reduced in exchange for both 

nolo contendere and guilty pleas, and as 

expected, engaging in the plea-bargaining 

process decreased one's chances of being 

sent to jail for both kinds of pleas. Those 

who came out of these negotiations having 

to plead guilty had a greater chance of 

going to jail than those who were able to 

enter nolo contendere pleas. Where plea 

bargaining did not take place, those who 

pleaded guilty had the highest chance of 

being imprisoned, those who pleaded nolo 

contendere had the least chance, and those 

who entered not guilty pleas were in the 

middle. 

It must be remembered that at least for our 

sample of 200 cases, almost all of the crimes 

against persons were considered to be 

relatively serious. Consequently, seriousness could not play much of a role in the 

dispositional process. Offender characteristics, on the other hand, varied but did not 

affect the chances of being jailed once the 

charge-reduction and plea process was 

taken into consideration. 

In sum, the dispositional dynamics for 

person and property crimes appear to be 

different, with plea bargaining having a 

much greater impact on the former than 

the latter. In neither case does the dispositional process appear to be biased once 

plea bargaining is incorporated into the 

analysis. What bias there is operates with 

respect to the defendant's previous record-and even here there is evidently a 

buffering process at work until the individTable 6. Estimates of the incarceration rates for crimes against persons 

' No change 	 Charge 

in charge reduced 

Guilty 78 48 

Plea Nolo contendere 39 14 

Not guilty 50 

Note: Estimated percentages are calculated from logit model: 

P.. log JL = p + ai+ pi l-pii 

Where P.. is the probability of incarceration. 11 

*No information in data 

-

ual's contact with the criminal justice 

system has become frequent and/or 

felonious. 

To argue that offender characteristics (sex, 

race, previous record) do not have a direct 

impact on incarceration rates for crimes 

against persons does not mean that they are 

not involved in the dispositional process. 

It's quite possible that a defendant's prior 

record, in conjunction with other indicators of his recidivism chances and the solidness of the state's case against him, set 

boundaries for the kinds of plea bargaining 

which can be struck. In our future investigations we will be examining these 

possibilities. 

This paper is an outgrowth of a workshop on criminal justice systems sponsored by the Social 

Science Research Council, July-August 1975. 

The authors would like to thank Leslie T. 

Wilkins for providing the data upon which this 

paper is based. 

References 

Bishop, Y. M. M., S. E. Fienberg, and 

P. W. Holland (1975) 

Discrete multivariate analysis. Cambridge, 

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Burke, Peter J., and Austin T. Turk (1975) 

"Factors affecting postarrest dispositions: A 

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Dyke, G. V., and H. D. Patterson (1952) 

"Analysis of factorial arrangements when the 

data are proportions." Biometries 9:l-12. 

Goodman, L. A. (1970) 

"The multivariate analysis of qualitative data: 

Interactions among multiple classifications." 

Journal of the American Statistical Association 

65:226-56. 

Haberman, S. J. (1974) 

The analysis of frequency data. Chicago: 

University of Chicago Press. 

Hagan, John (1975) 

"Law, order and sentencing: A study of attitude in action." Sociometry 38:374-84. 

Heumann, Milton (1975) 

"A note on plea bargaining and case pressure." Law & Socie!I. Review 9:5 15-28. 

Larntz, K. (1975) 

"Small sample comparisons of exact levelsfor 

chi-square goodness-of-fit statistics." Technical 

Report No. 242. University of Minnesota School 

of Statistics. 

Tiffany, Lawrence P., Yakov Avichai, and 

Geoffrey W. Peters (1975) 

"A statistical analysis of sentencing in federal 

courts: Defendants convicted after trial, 1967- 

1968." Journal of Legal Studies 4:369-90. 
The deterrent efsects 


of punishment 


Alternative estimates of the impact 

of certainty and severity of punishment 

on levels of homicide in American states 

COLINLOFTIN 

Department qj' Sociology and Center 

,for Research on Social Organization 

University qj' Michigan 

Jack Gibbs' paper, "Crime, Punishment, 

and Deterrence," has been widely cited as 

an important part of an accumulating body 

of evidence which consistently demonstrates a negative relationship between 

crime rates and the certainty and severity of 

punishment. In this paper we providea new 

set of estimates of the effects of the 

certainty and severity of punishment on 

homicide rates. The estimates are derived 

using a structural model of violent crime 

which was developed independently of 

Gibbs' research. When the effects of the 

other variables in the model are taken into 

account, the estimated effects of the 

punishment variables are very small. The 

data are consistent with a model in which 

certainty and severity of punishment have 

no effects on homicide rates. 

Background 

In 1968 Jack Gibbs presented the results of 

an influential study of the effects of certainty and severity of punishment on 

murder rates in American states. While he 

was appropriately cautious in interpreting 

his estimates as doing no more than challenging the "common assertion that no 

evidence exists of a relationship between 

legal reactions to crime and the crime rate" 

(Gibbs 1968529-530), subsequent discussions have interpreted his study as providing support for deterrence effects (see, for 

example, Tullock 1974:107, Tittle and 

Logan 1973, Antunes and Hunt 1973, 

Tittle 1975). Gray and Martin (1969) and 

Bean and Cushing (1971) reanalyzed 

Gibbs' data, with slight modifications in 

statistical procedures and theoretical model, and concluded that the data are consistent with a model which includes direct 

negative effects of certainty and severity of 

punishment on murder rates. More recent 

studies of the effects of law enforcement 

activity on crime rates have gone considerably beyond these studies in terms of theoretical specifications and estimation procedures. Nevertheless the estimates of 

deterrence effects from these early studies 

continue to be cited in current discussions 

as part of an accumulating body of evidence supporting the existence of general 

deterrence effects. In this paper we provide 

a new set of estimates using a model which 

was specified independently of Gibbs' 

research, and which includes a much larger 

number of etiological (or environmental) 

variables than do any of the other deterrence studies. When the effects of these 

etiological variables have been removed 

from Gibbs' measures of the certainty and 

severity of punishment, the estimated effects of the punishment variables are very 

small and provide reason to question 

whether the data provide any support for 

real effects of certainty and severity of punishment on homicide rates. 

Before presenting the new estimates it will 

be useful to briefly review the results of the 

other studies of Gibbs' data. Gibbs' original paper specifies the following general 

model for crime rates: 

where C is the crime rate; Erepresents etiological factors, that is, "extralegal conditions which are conducive to crime . . ." 

(Gibbs 1968517); and R represents repressive factors, that is "aspects of reaction to 

crime which operate as deterrents ..." 

(Gibbs 1968:517). However, his actual 

investigation of homicide rates fails to 

include any etiological factors. He estimates the relationship between the two 

repressive factors and homicide rates while 

ignoring etiological factors. The two 

repressive factors specified in the study are: 

(1) Estimated severity of sentence received and served for criminal homicide, 

which he measured with the median 

months served on a homicide sentence by 

persons in a state prison on December 31, 

1960 (Gibbs 1968:520-521). 

(2) Estimated certainty of imprisonment for criminal homicide, which he 

measured as the number of persons 

admitted to state prisons in 1960ona homicide sentence, divided by the average 

number of criminal homicides reported by 

the police in 1959 and 1960. The dependent 

variable is the average annual criminal 

homicide rate per 100,000 population for 

1959 to 1961.1 

Gibbs'statistical analysis is done with contingency tables by dividing each distribution at the median. From this analysis, he, 

concludes that both certainty and severity 

of punishment are negatively related to 

state homicide rates. 

'New Jersey's values for certainty and severity were 

estimated from the average of New York and 

Connecticut. 
Table 1. Selected results of previous analyses of Gibbs' Data 

Gray and Martin (1969) 

Bean and Cushing (1971) A 

(1) 	 H =_Po -.289 P(I) -.374 T + u 

p/sp = (-2.1 9) (-2.84) 

R' = .218 

A 

(2) H =!,_ -.I96 P(I)-2.05 T + .717 R + 

New estimates of certainty 

and severity of punishment 

on homicide rates 

Sociological theories of homicide, though 

not incompatible with utilitarian formulations which characterize most deterrence 

studies, suggest that homicide is an 

extreme manifestation of the "culture of 

violence" which is generated by high levels 

of personal frustration and extreme socioeconomic deprivation (Wolfgang 1958, 

Wolfgang and Ferracuti 1967, -~rearl~ 

1932, Coser 1967). Some crimes of violence 

may be incidental to participation in other 

forms of illegal activity, but most homicides are known to occur among friends, 

family, and acquaintances and are not by- u 	 products of other crimes (Wolfgang 1958, 

@/Sflo = (-2.39) (-2.33) (8.31) 1968). They are likely to be acts of passion 

13' = 596 that grow out of high levels of frustration 

A and subcultural reinforcement of interper- (3) 	 ~=p,_ -.I79 ~(1)- .I67 T+ .77 B + u sonal violence. B/spO= (-22.38) (-2.16) (9.87) 

A previous study by Loftin and Hill,
 R2 = .751 drawing on studies done by Gastil (1971) 


and Hackney (1969), specified a model 


Notes: The regression coefficients are for varialrles in standard form, that is, they are which is derived from sociocultural expla- beta weights. H = homicide rate, P(I) = probability of imprisonment (Gibbs' measure of certainty of punishment), T = median time served (Gibbs' measure nations of homicide rates. The key element 

of severity), R = region (South is coded I, nonsouth is coded 0). and B = percent in this model is a six-variable index 

of population black. Gray and Martin do not provide estimates of standard errors or t values. Their coefficient for P(I) in equation appears to be an error. referred to as an index of "structural 

Our own analysis is consistent with Bean and Cushing's results. poverty" which redundantly measures the 

-proportion of a state's population at the 

extremely low end of the socioeconomic 

Gray and art in (1969) extended Gibbs' substitute "percent of the population that is class distribution. The components of that 

study by investigating several different black" for "region" in their model and find index are: forms of the relationships between certain that the proportion of the variance (1) Infant Mortality Rate (Grove and 

ty, severity, and homicide in an ordinary "uniquely accounted for by the etiological Hetzel 1968: Table 41). least squares regression analysis. Table 1 factors" increased, and thus that the data 

are consistent with the hypothesis that the (2) Percent of persons 25 years old and summarizes the major elements of their 	 over with less than years of school analysis which led them to conclude that etiological significance of region is due to (Renetzky and Greene 1970:38). 
 the data are consistent with a model in percent black (Bean and Cushing 1971: (3) Percent of families with income
 which certainty and severity of punishment 288). under $1,000 (U.S. Bureau of the Census 


Operate in a nonadditive way reduce the Other studies which have estimated deter- 1964a:Table 137). 
 homicide rate (Gray and 19P9: rence effects for homicide, but which use (4) Percent of the population illiterate 
 394-395). Note that their invest1gat10n9'Ike data different from Gibbs, include Tittle (Greene and Renetzky 1970:38). 
 Gibbs'3 derived estimates of certainty and (1969), Chiricos and Waldo (1970), Antunes (5) Armed Forces Mental Test Failures 


severity effects under the assump- and Hunt (1973), Logan (1972, 1975), (August 1958-December 1965) (American 

that can be knored'Bailey, Martin, and Gray (1974). All of Education 1966:9). That etiological factors were these studies, except Logan (1975), esti- (6) Percent of children living with one included in the estimated model. mate significant negative deterrence ef- parent (U.S. Bureau of the Census 

Bean and Cushing (1971) recognized thk fects, but none of them includes more than 1964b368). 

importance of specifying a model which one variable to represent etiologicalfactors These variables account for 87 percent of 

allows for etiological as well as repressive and most of them do not include any etio- the variance in 1959-1961 mean homicide 

factors, but the models that they investi- logical variables. The major exception to rates in Loftin and Hill's analysis.' 

gated included only one etiological vari- this generalization is Ehrlich (1973, 1975), Hill,s homicide rate is based on the U.S. able at a time. They found that when a who reports several investigations of the Vital Statistics rather than on the uniform Crime 

variable representing region (South versus effects of law enforcement variables On Report and thus is slightly different from Gibbs' 

Nonsouth) was included in a linear specifi- homicide rates, all of which use models homicide rate. See Loftin and Hi11 (1974:718 and 720) 

cation (see Table 1 above), the estimates of which take into account more than one eti- fP,',"??~~",$Si$~~~ betweenthe two 

the certainty and severity effects were ological factor, and allow for simultaneous 

reduced, but that they were still large relationships between crime rates and law 

enough to be "consistent with the deter- enforcement variables. His results are 

rence hypothesis" (Bean and Cushing consistent with most other studies in that 

1971:289). Also they conclude that the his deterrence variables are negatively and 

linear specification which included region significantly associated with homicide 

was as adequate as alternative nonlinear rates.2 

'pecifications of the they -cent evaluations of Ehrlich's findings raise 

serious questions about the sensitivity of his results to 

minor changes in the model (see, for example, Bowers 

and Pierce 1975). 
I I probability of arrest and prosecution deTable 2. Correlations between Gibbs' measures of the homicide rate, the certainty of clines as the number of crimes increases punishment, the severity of punishment and the six components of the does not seem appropriate for the situation Loftin-Hill Index in the United States in about 1960. ConHomicide Certainty of Severity of 

rate punishment punishment 

Infant mortality rate (IMR) 

Percent of persons with less than 5 


years of education (LOWED) 


Percent of population illiterate 


(ILLIT) 


Armed forces mental test failures 


(TESTFAIL) 


Percent of families with less than 


$1,000 income (LOWINC) 


Percent of children living with one 
 parent (ONEPARENT) 


Table 2 shows the correlations between the. 

components of the index and Gibbs'three 

variables (homicide rate. certaintv -. of Dunishment, and severity of punishment). Note 

that the components are all positively correlated with the homicide rate and negatively correlated with the. certainty and 

severity of punishment. This suggests a 

model, which Gibbs acknowledges (1968: 

528) but does not investigate, in which 

sociocultural variables, such as those 

measured in the Loftin-Hill index (eriological factors in Gibbs' terminology), 

operate to increase homicide rates in some 

states and simultaneously to reduce the certainty and severity of punishment. Little is 

known about the determinants of variables 

such as Gibbs'certainty and severity, but it 

is plausible that they are reduced when a 

significant proportion of the population is 

extremely poor and uneducated, both because of the direct effects of the sociocultural factors and because of common 

causes. This suggests that estimates of 

deterrence effects, to the extent that they 

have not taken social and cultural variables 

into account, may have overestimated the 

size of these effects. 

The complete specification of the homicide 

model that Loftin and Hill use and which 

we will use in the present analysis includes 

six other variables: 

(7) Dye's Gini Coefficient of income 

inequality for American states (Dye 1967). 

(8) Region (a binary variable coded 1 

for former Confederate states, 0 otherwise). 

(9) Percent of population nonwhite 

(U.S. Bureau of the Census 1964a:Table 

56). 

(10) Percent of the population age 20 to 

34 (US. Bureau of the Census 1964b:23). 

(I I) Percent of the population living in 

rural territory (US. Bureau of the Census 

1964a:Table 21). 

-.222 -.332 

(12) Number of hospital beds per 

100,000 population (U.S. Bureau of the 

Census 196280). 

To derive our estimate of the effects of 

Gibbs' repressive factors we simply use 

Gibbs' homicide rate as the dependent variable and add his measures of the certainty 

and severity of punishment as independent 

variables, along with those used in the previous study (Loftin and Hill 1974). It 

should be noted that while there is an 

element of arbitrariness in the selection of 

the sociocultural variables to be included in 

the homicide model, the model that we use 

in this analysis was developed independently 

of research on deterrence, and thus no 

selection of variables which maximize or 

minimize the effects of the repressive 

factors was possible. -. ---

Our use of ordinary least squares regression analysis to estimate the parameters of 

the model implies that the homicide rate is 

not simultaneously determined with the 

sanction variables. While this may not 

generally be the case it is plausible that, at 

least in the case of homicide and for the 

range of variation represented by American-states in about (960, repressive variables are unresponsive to homicide rates. 

Homicide is a rare crime with a very high 

clearance rate. In 1959 the clearance rate 

for murder and nonnegligent manslaughter 

for all geographic divisions of the United 

States, according to the Uniform Crime 

Reports, was 92.7 with a standard deviation of only 3.1 across the nine Uniform 

Crime Reports' geographic divisions.4 

Large increases in the amount of. violent 

crime might reduce the effectiveness of 

police investigations and strain other resources of the criminal justice system, but 

the analogy with a riot situation where the 

"he data are based on 2094 cities with a toal population of 77,695,412 (Uniform Crime Reports 1959: 

Table 13, p. 83). The comparable figures for 1960 and 

1961 are 92.3 and 93.1 for the clearance rate; thestandard deviations are 5.9 and 4.1. 

temporary Northern Ireiand and Lebanon 

probably fit the model, but they represent 

very extreme cases far outside of the range 

of variation represented in Gibbs' data. 

It is also unlikely that judges, juries, and 

parole boards adjust sentences on the basis 

of the homicide rates. It is more plausible 

that these decisions are made primarily on 

the basis of judgments of the seriousness of 

the crime and the probability that offenders are committed to violent crime as a way 

of life, along with the particular circumstances of the crime (see, for example, 

Wilkins 1974:244-245). Thus the degree of 

criminal intent and extenuating circumstances as judged by juries and parole 

boards are probably the key factors, not 

the general level of homicide. 

Certainly general public sentiments and 

public opinion will have an impact on punishment levels, but again public opinion is 

probably responsive primarily to social 

and cultural variables rather than to the 

homicide rate. 

The hypothesis that homicide rates influence certainty and severity of punishment 

remains an open question which should be 

examined carefully in future research. Our 

argument is that, for our present purposes, 

it is just as reasonable to derive estimates 

assuming no simultaneous relationships 

'between homicide rates and repressive factors as it is to derive simultaneous estimates 

under the extremely restrictive assumptions that would be necessary for such an 

analysis. Without pursuing a detailed critique of simultaneous estimations that 

have been made in deterrence studies, it 

should be noted that many of-the variables 

that have been treated as instrumental vari-. 

ables and thus excluded from crime functions and included in punishment functions 

seem very arbitrary and inconsistent with 

existing theory. For example, it is not at all 

clear why such variables as region, percentage of the population that is nonwhite, age, 

and government expenditures should be 

excluded from crime functions, yet this has 

been the practice in existing studies that 

have made simultaneous estimates.5 

When one adds to these difficulties the fact 

that we are deriving our estimates with a 

relatively small number of observations (N 

= 48) and that simultaneous estimation 

procedures such as two-staged least 

sSee Nagin (1975) for a critical discussion. 
squares do not provide substantial im- I 

provements over direct ordinary least 1 Table 3. Ordinary least squares estimates of models which include only certainty and 

square estimates unless sample size is large 1 severity of punishment 

(Namboodiri et al. 197551 7). there seems A. Linear model H = Po + P1 P(l) + P2 T + u I 

to be no strong reason for expecting that 

simultaneous estimates will be superior to p^ pis; direct estimates. Certainty -.07036 -2.19053 

Severity -.062 -2.83778 Table 3 presents our estimate for two mod- Constant -14.93599 

els which contain only Gibbs' repressive 3 = .20144 factors. In both the linear and the multiplicative forms the estimates of the effects 

of certainty and severity of punishment are B. Multiplicative model H = fl0P(I)" TP2 e" negative and greater than twice their standard errors.-he d-statistic in Table 3 provides a means of comparing the goodness In Certainty of fit of the two models in terms of the 1n Severity 

residual sums of squares.' The multiplic- Constant - ative form clearly fits better than the linear R2 = .36509 

form; the residual sum of squares for the 

transformed linear model is almost twice as 

large as the multiplicative model, and the C. Comparison on linear and multiplicative models 

d-statistic is significant at well beyond the d = 13.35339 0.01 level. All of this is consistent with previous analyses of the data and is presented 

here as a basis of comparison with the estimate derived from the more complete Table 4. Ordinary least squares estimates of models which include certainty and severity 

forms of the model. of punishment along with components of the Loftin-Hill Index 

Estimates from linear and multiplicative A. Linear model H =Po + P1 P(1) + f12T + Pg IMR +. . .p8 ONEPARENT + u 

forms of a model which includes the six p^ -cs; components of the index used by Loftin 

and Hill along with Gibbs' repressive fac- Certainty -.01906 -1.112 

Severity 	 7.01340 -1.085 tors are presented in Table 4. In the linear IMR .31587 3.384 

form of the model the adjusted coefficient ' LOWED .84948 2.790 

of determination8 increases from 0.20 to ILLIT -2.34584 -2.812 

LOWINC 	 -.I8781 -1.380 0.83 when the index variables are added to TESTFAIL -.00557 w.095 

the model; in the multiplicative form the ONEPARENT .49164 2.153 

(Constant) 	 -6.84304 increase is from 0.37 to 0.78. More impor- - tant, however, for present purposes is the R2 = .83248 

reduction in the magnitude of the estimates Z el *2 = 6.01917 

of the punishment effects in both forms of 8. Multiplicative model H = P~P(I)~~T P 2 1 P3. ~ ~ . . ONEPARENT~~~U

the model. In the linear specification the 

estimated certainty effect falls from -0.070 p^ ;st 

to -0.019 and severity falls from -0.063 to Ln Certainty -.25591 -1.360 

-0.013. In both cases the estimated regres- Ln Severity -.53973 -2.725 

sion coefficients are considerably less than Ln IMR 1.39258 2.078 

Ln LOWED 1.46564 1.932 

6The multiplicative model is estimated by expressing Ln ILLIT -1.34457 -2.31 1 

Ln LOWINC 	 -. 16483 -.677 each variable in terms of its natual logarithm. In this Ln TESTFAI L .05066 .I90
 form the multiplicative model can be expressed as Ln ONEPARENT 1.37484 2.921 


InH = In& + PIInP(1) + /32 InT+ u.Subsequent multi- (Constant) -5.021 70 


plicative models are estimated in the same way. -


'To compute d the homicide rate was multiplied by a R2 = .78210 

constant, C, which is defined as C e2*2 = 5.64538 

C. Comparison of linear and multiplicative models 

d = 1.53868 


Then both models were estimated using the trans- 


formed homicide rate. The residual sums of squares 1 


are used to derive d as follows: \ 


twice their standard errors. In the multi- severity effect, we have examined the good- = 21In- Sei+'I plicative form the estimated effect of cer- ness of fit for the two forms in some detail. 

\'ef2 tainty falls from -0.852 to -0.256 and the The d-statistic indicates that although the 

The error sum of squares for the linear model is desig- estimated effect of severity from -1.269 to multiplicative form has a smaller residual 

nated Sef' and Sefyor the multiplicative model. See -0.540; only the severity estimate is more sum of squares (5.645 as opposed to 6.019 Rao and Miller (1971:107-1 I I) for a discussion of the 

procedure. 	 than twice its standard error. Since the two for the linear specification), the difference 

forms of the model lead to different con- is not significant at the 0.05 level. More- The adjusted coefficient is defined as clusions about the importance of the over, a plot of the residuals against the 

expected normal order statistics shows that 

there is one extremely deviant value for the 

where N is the total observations and k is the number multiplicative specification (the case is 

of parameters estimated, including the constant term. Rhode Island) and there is a noticeable 
deviation from a linear relationship near 

the lower end of the plot. Since there is no Table 5. Ordinary least squares estimates of models which include certainty and severity 

compelling theoretical reason for selecting of punishment and all of the Etiological variables 

the multiplicative specification and since A. LinearModel H=@o+PIP(I)+P2T+P31MR+ ...flI4GINI+~ 

there is evidence that the linear model fits 

the data at least as well as if not better than 

the logarithmic model, we are inclined to 

select the linear form as the better specification. Howevcr, as the next segment of our 

analysis will demonstrate, the choice 

between the linear and logarithmic specifications becomes less important in assessing 

the importance of the punishment variables when the other variables in the homicide model are introduced. 

In the analysis described in Table 5 we add 

the remaining six variables in the homicide 

model. With the exception of the estimation of the certainty effect in the linear 

specification, which remains essentially the 

same, the estimated effects of the punishment variables are reduced still further, 

and in no case are the estimates of punishment effects greater than twice their 

standard errors. Moreover, in the linear 

specification the estimate of the effect of 

severity of punishment has changed its sign 

from negative to positive. 

Since both forms of the model lead to the 

same general conclusions about the significance of the punishment variables, the 

selection between the linear and the multiplicative forms is less important than it 

appeared to be in the earlier specification 

(Table 4) where the form of the model 

made a difference in the significance of the 

severity estimate. The multiplicative form 

seems to fit a little better than the linear 

form but the d-statistic (2.467) isconsistent 

with the conclusion that they were drawn 

from the same population. 

It should also be noted that the reduction 

of the punishment effects to an insignificant size does not depend onenteringall 12 

of the etiological factors. We have already 

shown that in the linear specification the 

estimated repressive effects are less than 

twice their standard errors after the six 

components of the index are introduced. In 

a step-wise analysis of the multiplicative 

specification, percent nonwhite entered on 

the first step after the punishment variables 

and the six components of the.index had 

been entered. At that point the estimated 

severity effect is less than twice its standard 

error and remains there until all the variables in the model have entered (see Table 

6). 

-

p^ pjs; 

Certainty -.02276 -1.556 

Severity .00397 .349 

IMR ,18016 1.789 

LOWED .34358 1.151 

ILLIT -1.60651 -1.921 

LOWINC -.05938 -.319 

TESTFAIL .03874 .631 

ONEPARENT .30235 1.495 

NONWHITE .03865 .694 

RURAL -.01734 -.568 

AGE .60985 2.561 

HOSPBEDS -.00203 -1.81 1 

REGION -1.85923 -2.182 

GIN1 ,01676 .960 

(Constant) -14.93599 -

Fi2 = .89166 

Eel = 3.30905 

B. Multiplicative Model H = POP(I)'IT~~IMR~~. ..GIN1 '14eu 

p^ ;IS; 

Ln Certainty -.I8257 -1.126 

Ln Severity -.00721 p.032 

Ln IMR .73758 1.206 

Ln LOWED -.06035 -.077 

Ln lLLlT ,48048 -. 798 

Ln LOWINC -.05027 -.I34 

Ln TESTFAI L ,17835 .787 

Ln ONEPARENT 1.12196 2.757 

Ln NONWHITE .31237 3.532 

Ln RURAL .I7588 .810 

Ln AGE 2.31 579 2.179 

Ln HOSPBEDS p.38872 -1.404 

REGION -.03707 -.I95 

Ln GlNl 1.20806 .492 

(Constant) -15.37168

-

R~=.86442 

Xe2 *2 = 2.98574 

C. Comparison of Linear and Multiplicative Models 

d = 2.46752 

Note: REG1 ON was coded arbitrarily as a binary variable so it was not expressed as a 

logarithm in the multiplicative form of the model. It remained in its original form. 

Table 6. Ordinary least squares estimates of multiplicative model which includes the 

certainty and severity of punishment, the components of the Loftin-Hill Index, 

and percent of population nonwhite 

p^ $sp^ ___) 

Ln Certainty -.I3560 .857 

Ln Severity -.I8916 1.035 

Ln IMR 1.32200 2.381 

Ln LOWED .04173 .055 

Ln ILLIT -.54782 1.063 

Ln LOWINC .07524 .361 

Ln TESTFAIL .09962 .453 

Ln ONEPARENT 1.24587 3.187 

Ln NONWHITE .33250 4.344 

-

(Constant) -5.20431 

R~ = .85067 

The 12 eriological variables in the model the multiplicative specification three meet 

also generally have small estimated effects; this criterion (percent of children living 

only two estimates are greater than twice with one parent, percent of population livtheir standard error in thehear specifics- ing in rural territory, and percent age 20 to 

tion (percent age 20 to 34, and region); for 34). However, this is to be expected given 

the fact that the 12 e~iologicalvariables, to 

a very large degree, reflect a single socioeconomic dimension and thus represent 

redundant indexes which divide up the 

socioeconomic variance among themselves 
References 

on the set of other independent variables 

Variable taken as dependent 

IMR 

LOWED 

ILLIT 

LOWINC 

TESTFAI L 

ONEPARENT 

NONWHITE 

RURAL 

AGE 

HOSPBEDS 

REGION 

GIN1 

CERTAINTY 

SEVERITY 

resulting in small estimates of independent 

effects. The etiological factors are included 

to purge the punishment variables of their 

dependence on etiological factors so that 

their independent effects could be more 

clearly evaluated; thus the size of individual eriological effects is not important for 

present purposes. 

The pattern of high multicollinearity 

among the 12 eliological factors can be 

seen in Table 7 where the coefficient of 

determination has been calculated from the 

regression of each independent variable on 

the set of other (k-1) independent variables. 

Note that while the 12 eriologicalvariables 

are very highly intercorrelated with each 

other (the average R2 is 0.84), the repressive 

factors are not highly correlated with each 

other (r2 = 0.00052) or with the other independent variables (R2 = 0.341 for certainty 

and 0.487 for severity). This indicates that 

the relatively large standard errors of the 

estimates of the repressive variables are not 

a result of multicollinearity and provides 

support for the inference that the punishment variables do not have independent 

effects on the homicide rate. 

Conclusions . 

Our purpose in this paper has been to show 

that when the effects of sociocultural factors are removed from Gibbs' measures of 

certainty and severity of punishment, the 

estimates of their independent effects on 

homicide rates are reduced to the point that 

they might reasonably be considered to be 

nonexistent. Such a demonstration is very 

important because previous, widely cited 

analyses of the same data have concluded 

that they provide evidence for independent 

deterrent effects. One should not conclude, 

however, that the data provide very strong 

evidence for either position. The analysis 

must remain inconclusive because of serious theoretical and methodological limitations on the research design. Gibbs himself, 

after a recent, thorough review of deterrence studies, concluded that ". .. horrendous problems preclude a categorical 

Table 7. Coefficients of determination (R~)for regression of each independent variable 

Coefficient of determination 

R2 

.85667 

.98837 

.98011 

.94671 

.95816 

.89702 

.9 1490 

.79563 

.60534 

.49285 

.79129 

.88510 

.34090 

.48702 

rejection or acceptance of the deterrence 

doctrine." (Gibbs 1975:l) We do not 

attempt to discuss these problems here. 

Excellent discussions are available elsewhere (Gibbs 1975, Nagin 1975, Greenberg 

1975). Our objective has simply been to 

demonstrate that the application of reasonable statistical estimation procedures to a 

model that adequately controls for sociocultural variables can provide evidence 

that is quite different from that provided by 

previous analyses of Gibbs' data. 

A cknow~ledgments 

The original work on this paper began in the 

Working Group on Deterrence Research at the 

Workshop in Criminal Justice Statistics which 

consisted of David Britt, Kinley Larntz, Colin 

Loftin, Dan Nagin, and David Seidman. At var- ious points other members of the workshop 

made important contributions to my thinking. 

The original calculations for the research were done in Washington during the workshop, but 

all calculations have been repeated with the original Loftin-Hill data rather fhan the data that were hastily collected during the workshop. I 

spent two days visiting with Kinley Larntz and 

Stephen Fienberg at the Department of Applied 

Statistics of the University of Minnesota. That 

experience had a major influence on the paper as well as on my general education. Michael 

Timberlake and Robert Parker, students in the 

Department of Sociology at Brown University, 

assisted with some of the data analysis presented 

in the paper. 1 am responsible for thedraft of the 

report and any errors that it contains. 

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Recent econometric modelling of crime 

and punishment: Support for the 

deterrence hypothesis? 

STEPHENS. BRIER 

Department of Statistics 

University of Iowa 

STEPHENE. FIENBERG 

Department of Statistics 

and Deparment of Social Science 

Carnegie-Mellon University 

In this paper we review some recent 

attempts to develop econometric models 

for assessing the deterrent effect of punishment on crime, as well as analyses carried 

out to validate these models. The formulation of the basic econometric model considered here is due to Becker (1968), and 

the detailed specification of the model, 

along with much of the empirical work reviewed, has been carried out by Isaac 

Ehrlich. We find serious flaws with the 

Becker-Ehrlich model, with the data used 

in its empirical implementation, and with 

Ehrlich's conclusions regarding evidence to 

support the deterrent effect of punishment 

on crime. Indeed, we can find no reliable 

empirical support in the existing economics 

literature either for or against the deterrence hypothesis. 

Introduction 

The threat to person and property from 

crime is a central problem of social concern 

in the United States today. But crime is not 

a new problem. "Crime in the streets" and 

"the need for law-and-order" have been 

slogans used by politicians at least since the 

early 1960's to exploit popular fears of 

crime, and the study of crime as a social 

phenomenon has played a prominent role 

in American sociology throughout the 

twentieth century. With the surge in reported crime in the 1960's, considerable 

public attention was focused on the control 

of crime through President Lyndon B. 

Johnson's Commission on Law Enforcement and Administration of Justice and 

the subsequent implementation of the 

Commission's recommendations. At the 

same time economists began to study law 

enforcement as an economic problem involving the allocation of scarce resources 

(e.g., see Becker 1968). 

Copyright @ 1980 by Sage Publications, Inc. Reprinted 

by permission, with minor changes, from Evaluation 

Revieu'. VOI. 4, NO.2, April 1980, pp. 147-191. 

The punishment of criminal offenders has 

played an important role in both the economic and sociological approaches to the 

control of crime. Although retribution was 

long considered to be a primary rationale 

for punishment, this view has given way, at 

least partially, to the position that punishment of offenders will lead to a subsequent 

reduction in or prevention of crime. The 

possible mechanisms for the prevention of 

crime through punishment, other than retribution, are several: 

(1) Incapacitation. By removing an offender from society for some period of 

time, we can prevent that offender from 

repeating his offense or committing other 

ones while he is not in contact with society. 

(2) Education. By administering punishment for antisocial acts (such as'crimes), 

government and its agencies achieve a 

moral and educational effect on individuals in general. Society thus instructs that 

these crimes are counter to its norms, and 

by doing so educates individuals and influences their behavior. 

(3) Rehabilitation. Through the use of 

education, correctional "treatment," or 

vocational training during imprisonment, 

society attempts to "change" offenders so 

that they will not commit crimes in the 

future. 

(4) Deterrence. By enforcing punishment on an offender, society warns the 

offender, and the community at large, and 

thus inhibits the offender or others in the 

community from engaging in criminal activity in the future. 

When it is the sanctioned offender who is 

inhibited from committing crimes by the 

actual experience of punishment we speak 

of specific deterrence; when individuals 

other than the sanctioned offender are so 

inhibited we speak of general deterrence. 

With regard to the deterrent effect of punishment we need to make a further distinction, suggested by Zimring and Hawkins 

(1973). between absolute and marginal 

deterrence: 

The problem of absolute deterrence relates to the 

question, does this particular criminal sanction 

deter? The problem of marginal deterrence re- lates to such questions as, would a more severe penalty attached to this criminal prohibition more effectively deter? In the capital punishment 

debate the issue is not that of absolute deterrence-whether the death penalty is a deterrent. 

It is that of marginal deterrence-whether it is a 

more effective deterrent than the alternative 

sanction of long imprisonment.1 

Most people can accept the notion of the 

absolute deterrence effect of many forms of 

punishment. For example, the removal of 

all sanctions for a crime such as robbery, 

most would agree, would lead to an increase in the rate at which robberies are 

committed; others might argue that the 

reason for the increase is not the removal or 

threat of punishment but rather the removal of the educational and moral value 

the punishment provided for society as a 

whole. The issue which is explored in this 

paper and which has been the subject of 

recent concern is that of marginal deterrence, i.e., we are interested in the potential 

effects of shifts in the level of sanctions on 

subsequent criminal behavior. 

Measuring the effects of these different 

mechanisms through which punishment 

might prevent crime is a far more difficult 

task than it may at first seem. As we just 

noted, it is often difficult to separate the 

educational and general deterrent components of the effects of punishment. Similarly, it is difficult to separate out the effects 

of incapacitation from those of deterrence. 

The difficulty is in fact one of explaining 

'Zimring and Hawkins (1973: 14). 
exactly what the mechanism of incapacitation actually entails. 

A simple-minded argumerit to explain the 

effect of incapacitation might go as follows. Suppose we imprison a 20-year-old 

male for a period of 2 years for committing 

the crime of burglary. Then, if that offender 

had been committing burglaries at the rate 

of, say, 12 per year, the simple fact of his 

removal from society for 2 years will prevent the commmission of 24 burglaries. 

Then, in any modelling we do, we would 

wish to remove these 24 burglaries from the 

overall effect of the 2 years of punishment 

on the future burglary rate. 

Even if we knew the rate of offending for 

each imprisoned offender, the calculation 

in this argument may completely distort 

the actual effects on the overall crime rate 

of incapacitating various individuals. In 

the case of the 20-year-old burglar, we need 

to know more about the nature and circumcumstances of his offenses. If he were a 

member of a group of burglars, all of whom 

work together, then his imprisonment may 

not have any effect at all on the number of 

burglaries committed by the group. Indeed, 

if he was arrested and convicted because he 

was the worst burglar in the group, the 

other members of the group might well recruit a superior replacement or simply increase their criminal activities, and thus the 

overall number of burglaries the group 

commits could easily increase. Cook(1977) 

discusses this replacement effect in an economic context in terms of its relationship 

to the quality of crime opportunities. Reiss 

(1980) has argued persuasively that the 

interpenetrating social networks of offenders and their victims need to be better 

understood before we can make any serious attempt to separate out the effects of 

incapacitation from those of deterrence. At 

the same time no empirical model for measuring the deterrent effect of punishment 

can be complete unless it also includes the 

related incapacitation effect in some form. 

(See also the discussion of incapacitation in 

the report of the National Academy of 

Sciences Panel on Research on Deterrent 

and lncapacitative Effects (Blumstein et al. 

1978).) 

Let us explore the mechanism of deterrence 

somewhat further. The effects of deterrence can be thought of only in the context 

of those who are likely to commit a crime 

and who are influenced by the threat of 

punishment for that crime if apprehended 

and convicted. The nature and extent of 

punishment can have no effect on those 

who do not need to be deterred from criminal activities and on those who are not or 

cannot be deterred by the threat of punishment. Thus, to measure the deterrent effect 

of punishment, we need to attempt to get at 

those on the margin of criminal activity. 

The size of the group of individuals on the 

margin limits the potential deterrent effects 

of any form of punishment. Since economic theory so often deals with the marginal effects of various policy changes, the 

appeal of crime and punishment as an 

application of economic modelling is great. 

What remains to be seen is whether such 

economic models are consistent with empirical observations. 

In this paper we review some recent attempts to develop econometric models for 

assessing the deterrent effect of punishment on crime, as well as analyses carried 

out to validate these models. The first section discusses the possible types of empirical investigations that might be used to 

study deterrence. Next we briefly describe 

the Becker-Ehrlich econometric model for 

crime and punishment. Then we describe 

some of the general problems in the empirical implementation of this model. The 

next two sections outline the pliblished empirical tests of the model along with some 

of our own reanalyses. One deals with 

cross-sectional data for 1960 and 1970, 

while the other deals primarily with longitudinal data for homicide and includes a 

special look at the deterrent effects of capital punishment. 

Finally our own conclusions regarding the 

empirical evidence on deterrence are presented. They can be summarized briefly as 

follows: 

(I) The Becker-Ehrlich model has glaring shortcomings and, when examined critically, does not lead to the claimed testable 

hypotheses regarding the effect of punishment of crime. 

(2) The use of the Becker-Ehrlich model 

for aggregate data requires extensive justification that has never been given. 

(3) The crime and imprisonment data 

used to empirically examine the BeckerEhrlich model are so untrustworthy as to 

render any serious analysis meaningless. 

(4) The empirical implementations of 

the Becker-Ehrlich model are badly flawed 

and have extremely grave statistical shortcomings and most published conclusions 

from them are not to be trusted. 

(5) Even if one accepts the BeckerEhrlich model, and Ehrlich's choice ofdata 

to implement it (which wedo not), Ehrlich's 

affirmative conclusions regarding the deterrent effect of punishment on crime in 

$.eneral, and of capital punishment on murder in particular, do not stand up to careful 

statistical scrutiny. 

Thus our conclusions are in agreement 

with those of the National Academy of 

Sciences Panel on Research on Deterrent 

and Incapacitative Effects: There is no empirical evidence to warrant an affirmative 

conclusion regarding the deterrent effect of 

punishment in general, and the available 

correlational or observational studies on 

homicide provide no useful evidence on the 

deterrent effect of capital punishment. The 

only available evidence that give support 

for the notion of general deterrence comes 

from "natural experiments" such as Ross's 

(1973) study of the British Road Safety Act 

(see the discussion in Cook 1977). Moreover, given the limitations of aggregate 

data on crime and incarceration, we believe 

that much more attention in the future 

should be focused on studies of individual 

criminal behavior. We do not expect any 

empirical research, at least in the near 

future, to provide definitive evidence on 

the deterrent effects of capital punishment. 

Possible vehicles 

tor studying deterrence 

As with many other social ohenomena. the 

relationship - between p;nishment 'and 

crime can, in principle, be explored either 

in an experimental setting or by an observational study. 

In a randomized controlled field trial, experimental units-individuals, collections 

of individuals, political or legal jurisdictions, etc.-are randomly assigned to treatment grovps and are then carefully 

followed to assess the actual effects of the 

treatment. The randomization allows the 

experimenter to avoid the dangers of selfselection, and it allows for the control of 

variables not included directly into the design of the field trial. The "controlled" 

nature of such field trials implies that the 

choice of treatment for an experimental 

unit is that of the investigator and that at 

least two treatments (or levels of treatment) 

are being compared (see Gilbert, Light, and 

Mosteller 1975) for further discussion). 

The randomized controlled field trial is the 

most demanding of all research strategies 

for investigating social innovations, but the 

increased reliability gained from a randomized trial can often far outstrip the costs. 

For a field trial involving deterrence the 
treatments would involve different levels of 

punishment and/or the threat of punishment. Unfortunately, there have been few 

examples of randomized controlled field 

trials dealing with deterrence. Zimring and 

Hawkins (1973) note that "[ilt is difficult to 

conceive of an acceptable experiment in 

which, after random assignment, the severity of sanctions threatened for a violation 

of a particular criminal law was varied 

betweenJhe two groups." While we do not 

completely agree with their statement, we 

do recognize the many legal and possibly 

moral roadblocks to careful experimentation on deterrence. Because of this difficulty in mounting experiments, most investigators resort to alternative research strategies, two of which are highly prominent. 

In the first approach the researcher attempts to assess the effect of a change in the 

level of sanctions by comparing reported 

crime rates before and after the change in a 

given jurisdiction. To reduce the potential 

biases and errors of such an approach, investigators often compare the change in 

rates with those in other jurisdictions 

where no changes in the level of sanctions 

took place. For a recent discussion of such 

"natural" experiments with regard to the 

deterrent effect of capital punishment, see 

Baldus and Cole (1975); with regard to 

other deterrent effects, see Cook (1977) and 

Zimring (1978). 

The other approach to the measurement of 

deterrent effects of punishment is the gathering of aggregate data on crime and punishment as well as on various social and 

economic variables. The researcher then 

studies the variations in crime that occur 

either among jurisdictions or over time. 

This is the approach adopted by Ehrlich 

(1973, 1975a, 1977b) in his attempt to develop an econometric model for the effect 

of varying sanctions, and the inherent difficulties in this approach are the primary 

subject of this paper. 

The Becker-Ehrlich model 

for crime and punishment 

Becker (1968) introduces his attempt to 

model crime and its optimal control by 

noting that "'crime' is an economiCally important activity, or 'industry', not withstanding the almost total neglect by economists." His model involves basically five 

behavioral relationships which he claims 

underlie the costs of crime-the relations 

between: 

(1) The number of offenses and their 

cost. 

(2) The number of offenses and the punishments meted out. 

(3) The number of offenses, arrests, and 

convictions and the public expenditures on 

police and courts. 

(4) The number of convictions and the 

cost of imprisonments or alternative punishments. 

(5) The number of offenses and the 

private expenditures on protection and 

apprehension. 

We do not discuss (5) any further here since 

it plays no role in Ehrlich's empirical implementation of Becker's model nor in the 

bulk of the related literature we consider. 

Becker's basic premise is that criminals 

maximize their expected gains (according 

to some utility function) from illicit activity. A person commits an offense if the 

expected utility he will receive exceeds the 

utility he would receive by engaging in 

other activities. Thus the criminal's decision is based on benefits and costs of both a 

monetaryeand psychic nature. According 

to Ehrlich (1973) an individual allocates a 

fixed amount of time among legal and illegal income-generating activities. The 

effects of this time allocation are introduced only implicitly by Ehrlich through 

the effects of time allocation on wealth. 

From the basic model Ehrlich goes on to 

derive some behavioral implications, such 

as: An increase in the probability of apprehension and punishment, with no change in 

other variables, reduces the incentive to 

participate in illegitimate activities. 

Block and Heineke (1975) have examined 

Ehrlich's model with great care and have 

shown that if the allocation of time is introduced explicitly into the utility analysis, the 

behavioral implications of the model derived by Ehrlich do not necessarily hold. 

Moreover, they note that, contrary to the 

assumptions of Becker and Ehrlich, it is not 

necessarily true that monetary equivalents 

to labor and penalty attributes of an offense exist. As a result, propositions regarding the deterrent effect of punishment 

become empirical questions rather than 

theoretical consequences subject to empirical validation. 

Implicit in the utility analysis of Becker, 

Ehrlich, and others is the assumption that 

criminals or potential criminals are rational 

decisionmakers in that they make their decisions according to a list of axioms. The 

appropriateness of such an economic 

model of crime is clearly open to question. 

For example, Avio and Clark (1976) state 

that: "It would be difficult to argue that 

perpetrators of violent crimes behave 

according to the usual set(s) of axioms. .. . Murders involving some form of premeditation and motivated by economic gain 

might be consistent with the economic 

model. Most murders, however, occur in 

the home, involve members of the same 

family, and seem unpremeditated." 

The net result of this econometric modelling is a functional relationship between the 

number of offenses committed by individualj, O,, and-

(a) his probability of conviction, p,, 

(b) his punishment given conviction,f;, 

(c) his rate of return (benefits) if he successfully commits the crime, w,,(istands for 

illegal returns), 

(d) the rate of returns from alternative 

legal activities, w~,(I stands for legal returns), 

(e) the probability of legal unemployment, UI,,and 

(f) a vector of other variables, v,: 

The function (1) is the one discussed by 

Ehrlich (1973), and is simply an elaboration of Becker's supply-of-offenses function. To arrive at (I), one must adopt many 

untested and possibly untestable assumptions regarding criminal behavior and its 

determinants. 

There is little or no discussion by Becker or 

Ehrlich regarding those "economic" variables not included in (I). Nor do they provide support for the forms of the variables 

appropriate for inclusion for the empirical 

validation of the model. This is a serious 

matter. No amount of utility theory, systems of partial differential equations, 

Kuhn-Tucker first-order optimality conditions, and analogies to the supply and 

demand for bread and butter (see Ehrlich 

and Gibbons 1977) can make up for the 

logical leaps that lead to the specification 

of (1). 

The first step adopted by Ehrlich and 

others in making the model of expression 

(I) suitable for empirical examination is 

the aggregation of data across individuals. 

Thus Ehrlich uses the aggregate function 

where 0*is the aggregate number of offenses in a particular jurisdiction,p* is the 

aggregate probability of conviction, and so 

on. The justification for such aggregation. 

typically rests on the assumption that either 
the parameters used to specify the relation 

(I) are constant across individuals or the 

parameters are stochastic, coming from 

some common distribution. Actually, to 

justify the aggregation, one needs further 

to specify a specific functional form. For 

example, suppose log O; is linearly related 

to the logarithms of the variables on the 

right-hand side of (1). Then, if the coefficients are the same across individuals, the 

aggregate number of offenses, O*, is 

related to the geometric means of the individual values for the other variables. Thus 

the justification of functional form must 

ultimately be established at the individual 

rather than the aggregate level. Since 

aggregation also takes place over time, we 

need to assume some form of constancy or, 

at a minimum, stochastic stationarity of 

the parameters in the functional specification (see e.g., Kuh and Welsch 1976). 

One of the few empirical examinations of a 

related functional specification at the individual level was carried out by Witte (1977). 

Her analyses show the importance of the 

specification of individual sociodemographic variables, such as race and age, and 

are supportive of arguments indicating the 

inappropriateness of the aggregate data 

used by most investigators in this area. 

Alternatives to the Becker-Ehrlich model 

exist. These are based on concepts such as 

the saturation of the resources of the criminal justice system (Cook 1977), and 

"homeostasis,"the apparent stability of imprisonment, and effective prison capacity 

(Blumstein and Cohen 1973; Nagin 1977). 

While we do not directly discuss the empirical examination of these alternatives, we 

note that they cast doubt on Ehrlich's 

claims regarding marginal deterrent effects 

of punishment. 

Moving toward empirical examination 

of the Becker-Ehrlich model 

To move from the aggregate supply-ofoffenses model of expression (2) to an empirical study of deterrence, one needs to 

(a) Specify in detail the "other" variables to be included as part of the vector v*. 

(b) Describe how the variables are to be 

measured. 

(c) Specify the actual functional form of 

the relationship. 

Ehrlich (1973, 1975a) provides a priori 

specifications for (a) and (c) which we call 

into question in our reanalysis of his data. 

Thus we defer our discussion of these matters to later sections of this paper. In this 

section we discuss (b). 

The actual rate of, ding in any community for any specific .ne during a specific 

time period is not Known. What we have 

available are data on offenses reported to 

the po!ice. As a substitute for 0* (the 

actual offense rate), Ehrlich (1973, 1975a) 

uses Q/N, where Q is the number of offenses reported to the police and recorded 

by them for a jurisdiction, and N is an estimate of the population size for that jurisdiction. It is well known that not all 

offenses committed are reported to the 

police. Estimates of the ratio of Q to Q*, 

the true number of offenses, vary from as 

low as 10 percent for rape to close to 100 

percent for murder. In the case of automobile theft there have been occasional reports that Q exceeds Q* because of nonthefts reported to the police for insurance 

purposes. 

Unfortunately, the ratio of Q/Q* can vary 

dramatically from jurisdiction to jurisdiction. For example, Skogan (1976) notes 

that in the 26 city victimization surveys 

conducted under the auspices of the National Crime Survey Q**/ Q*(where Q** is 

the number of crimes reported to the 

police) for robbery varied from 52 percent 

to 76 percent.2 The estimates of the ratio of 

the number of crimes appearing on police 

records (i.e., Q) to the number actually 

reported (i.e., @*) for these 26 cities, 

however, varied from 19 percent to 100 

percent! 

The quantity Q is also used by Ehrlich to 

get a measure of p*, the aggregate subjective probability of punishment (i.e., apprehension and imprisonment). He uses C/ Q 

as an estimate ofp* where Q is the number 

of recorded crimes in a given period of time 

and C is the number of offenders imprisoned during the same time period for the 

same jurisdiction. There are three problems 

here. 

First, C and Q involve different units. C 

deals with offenders, and Q deals with 

offenses. There is not a one-to-one correspondence between the two. 

Second, for a fixed period of time and a 

given jurisdiction, it is impossible to determine which of the offenses that are included 

in Q ultimately lead to apprehension and 

imprisonment. For example, juveniles are 

'These rates are subject to substantial sampling error, 

and some of the variability can be attributed to this 

source. 

usually handled by separate juvenile justice 

systems and are rarely sent to prison. Individual offenders are not tracked over time 

through the criminal justice system, and 

the aggregate figures for those imprisoned 

that are available for jurisdictions such as 

states include individuals whose crimes 

may have been committed in other states. 

These aggregate figures also include 

offenders whose crimes took place possibly 

several years prior to incarceration. Thus 

the use of contemporaneous values of C 

and Q by state can lead to sizeable discrepancies between C/ Q and p*, which can be 

shown to vary from state to state in occasionally very strange ways. We discuss this 

problem further in the next section. 

Third, Q now appears on both the left- and 

right-hand sides of the operational version 

of equation (2). As is noted in the report of 

the National Academy of Sciences (Blumstein et al. 1978), variation in the error in 

measuring Q*, the true number of crimes 

committed, can induce a spurious negative 

relation between the offense rate and the 

punishment rate, when no such relationship 

actually exists. Klein, Forst, and Filatov 

(1978) demonstate how such errors can 

induce a similar bias in the estimated relation between murder and execution rates. 

The source of the data used by Ehrlich and 

others to analyze the deterrent effects of 

punishment in the United States is the Uniform Crime Reports (UCR) produced by 

the Federal Bureau of Investigation (FBI). 

UCR data are collected as part of a voluntary reporting system involving state and 

local law enforcement agencies and are 

based on crimes recorded by these agencies. 

In addition to the problems of reporting 

and recording offenses noted earlier,UCR 

rates may seriously distort the level of 

offenses because multiple crimes with possibly multiple victims often are recorded as 

single offenses, and conversely single criminal events often involve multiple offenders, 

etc. 

Since the beginning of the UCR program in 

1933, both the number and the percentages 

of law enforcement agencies reporting to 

the FBI have increased dramatically. 

Moreover, reporting practices have also 

evolved, and officials generally agree that a 

larger proportion of offenses made known 

to the police now get reported to the FBI 

than was the case in the past. Finally, 

although the proportion of units reporting 

has increased over time, specific police departments that are once included in the 

UCR data base may not be included at later 

points in time. 
1 

Table 1. Variables used in Ehrlich's analysisa 

63 : Crime rate (the number of offenses known per capita) 

: Crime rate lagged one year 

: Estimated probability of apprehension and imprisonment (the number 

of offenders imprisoned per offenses known) 

: Average time served by offenders in state prisons 

: Median income of families 

: Percentage of families below one-half of median income 

: Percentage of non-whites in the population 

: Percentage of all males in the age group 14-24 

: Unemployment rate of civilian urban males aged 14-24 and 35-39, 

respectively 

'-1 4 : Labor-force participation rate for civilian urban males ages 14-24 

Ed : Mean number of years of schooling of population 25 years old and over 

SMSA : Percentage of population in standard metropolitan statistical areas 

: Per capita expenditure on police in fiscal 1960, 1959, respectively 

M : Number of males per 100 females 

D 	 : Dummy variable distinguishing northern from southern states 


(south = 1) 


a~ subscript j denotes that the variable is indexed by specific crime categories. 

The UCR data used by Ehrlich for his 

cross-sectional analyses (discussed in the 

next section) are based on the UCR for the 

years of interest. The data used in his national longitudinal analysis of murder (discussed later) are not the reported rates for 

each point in time. Rather, they consist of 

FBI estimates of what the reported crime 

rates would have been had the units included in the UCR system been the same as 

in 1972. Unfortunately there is no published 

description of the procedure used by the 

FBI to reestimate the rates. We have no 

way to assess the appropriateness of the 

FBI's reestimation procedure, but it is 

reasonable to conclude that it is likely to 

add further biases and increased variability 

to an already poor measure of crime. 

We do not believe that UCR data collected 

prior to 1960 merit serious attention since 

are completely 

are subject to enormous errors and biases. 

Any substantive conclusions one might 

draw from the analysis of these data are not 

be trusted' Even Ihe longer Wishes data prior 1960because 

of doubts regarding their We 

have serious reservations regarding the 

quality and validity of the 1960 UCR data 

used by Ehrlich and others. Nonetheless, we discuss the 1960 data and national longitudinal UCR data for murder from 1933 

through 1969 in the following two sections. 

One alternative to the use of UCR data is 

the use of data from the special city surveys 

associated with the National Crime Survey 

(see Penick and Owens 1976). Cook (1977) 

and Wilson and Boland (1976) have used 

NCS city data to examine the effects of 

sanctions on the crimes of burglary and 

robbery, respectively. Cook (1977) insome 

simple preliminary analyses shows that the 

"usual" negative correlation between the 

UCR reported burglary rates and the corresponding UCR clearance rates is greatly 

diminished when city data from the NCS 

are used in their place. The Wilson and 

Boland (1976) study, which does find a significant negative effect using NCS data for 

robberies, unfortunately suffers from many 

of the methodological flaws discussed in 

the remaining sections of this paper. Given 

the serious technical problems with the 

NCS city data (see Penick and Owens 

1976), we do not see the use of victimization data as a way of correcting the problems associated with UCR data. 

The analyses of U.S. crosssectional crime data 

I,., this section we discuss some recent analySeS that have attempted examine the Becker-Ehrlich econometric 

model of crime and punishment using 

cross-sectional data for the United States. 

We have attempted to replicate some of 

these results, and we report on our findings 

in this regard along with some additional 

analyses. 

e 

1 	Ehrlich S 1960 data 

Ehrlich (1973) analyzed data from 47 

states. The states omitted from theanalyses 

were Alaska, Hawaii, and New Jersey (see 

Vandaele 1978). New Jersey was omitted 

because certain key variables could not be 

obtained. The listing and definitions of all 

variables used in Ehrlich's study are given 

in Table 1. 

To implement the aggregate model of 

expression (2), Ehrlich chose to use a 

Cobb-Douglas production function of the 

form 

I where Q/N is the operational attempt to 

estimate the offense rate. O*. 

C/N is the operational attempt to 

estimate the probability of 

punishment, p*. 

T*, the average time served by 

prisoners in state prisons, is 

the empirical measure off*, 

the punishment given conviction. 

W, the median family income, 

and X, the percentage of families below the median income, 

are used as replacements for 

the differential monetary returns of crime relative to legal 

alternatives, i.e., w,* and WI*. 

VII, the male urban unemployment 

rate for ages 14-24, and LI4, 

the labor force participation 

rate for this same group, are 

used in lieu of ul*,the probability of legal unemployment. 

NW, the percentage of nonwhites, 

and A14, the percentage of 

males in the 14-24 age group, 

are the "other variables," v*. 

a, and b, for i = 1, 2, . . . ,8, are 

parameters to be estimated. 

e is a random error term. 

The relationship among the variables in (3) 

is multiplicative, and we must take logsrithms of both sides of the equation to pro- duce linearity (we use natural logarithms, 

denoted by 

(g) = bo + blln (g)+ b21nT* 

+ b~lnW + bJnX (4) 

+ btln V14 + bhlnL14 

+ bllnN W + bslnA14 + e. 

(Here we take b~ = lna.) As a result of a 

variety of statistical analyses, Ehrlich concluded that v1.1, L14, and AIJ had virtually 

no effect on the rest of the estimated equation and so he dropped them to yield the 

model: 
- - -- 

C 

Table 2. Estimated coefficients of selected variables in equation [51. Estimates obtained 

by two-stage least squares 

Offense Intercept (C/O)i Ti' W X NW 

Robbery -1 1.030 -1.303 -0.372 1.689 1.279 0.334 

(-1.804)a (-7.01 1) (-1.395) (1.969) (1.660) (4.024) 

Burglary -2.121 4.724 -1.127 1.384 2.000 0.250 

(-0.582) (-6.003) (4.799) (2.839) (4.689) (4.579) 

Larceny -1 0.660 -0.371 -0.602 2.229 1.792 9.142 

(-2.195) (-2.482) (-1.937) (3.465) (2.992) (2.019) 

Auto theft -14.960 -0.407 -0.246 2.608 2.057 0.102 

(4.162) (4.1 73) (-1.682) (5.194) (4.268) (1.842) 

Property crimes -6.279 -0.796 -0.915 1.883 2.132 . 0.243 

(-1.937) (-6.140) (4.297) (4.246) (5.356) (4.805) 

Murder 0.316 -0.852 -0.087 0.175 1.109 0.534 

(0.085) (-2.492) (-0.645) (0.334) (1.984) (8.356) 

Rape -0.599 -0.896 -0.399 0.409 0.459 0.072 

(-0.120) (-6.080) (-2.005) (0.605) (0.743) (0.922) 

Assault -7.567 -0.724 -0.979 1.650 1.707 0.465 

(-1.280) (-3.701 ) (-2.301 ) (2.018) (2.1 11 ) (3.655) 

Crimes against 1.635 -0.803 -0.495 0.328 0.587 0.376 

the person (0.380) (-6.603) (-3.407) (0.570) (1.098) (4.833) 

All offenses 	 -1.388 -0.991 -1.123 1.292 1.775 0.265 

(-0.368) (-5.898) (4.483) (2.609) (4.183) (5.069) 

umbers in parsntheses are t-ratios (i.e. the estimated coefficients divided by their 


estimated standard errors). 


are obtained by two-stage least squares 

(using a weighting scheme) and also by the 

method of "seemingly unrelated regressions" 

due to Zellner (1962). In all cases the coefficient of most'interest, b~, has a negative 

Ehrlich uses a simultaneous equations ap- estimate and is judged to be significantly 

proach to estimate the coefficients in equa- different from 0 (based upon its t-ratio 

tion (5) in which the crime rate (Ql N), the being larger than 2). We give Ehrlich's twoprobability of imprisonment (CIQ), and stage least squares estimates of the coefthe amount of police expenditures per ficients in Table 2. 

capita (El N) are simultaneously deter- Ehrlich's final conclusion, based on the 

mined or endogenous variables. Ehrlich analyses just outlined, is that these 1960 

does not present a system of structural data provide strong support for the theory 

equations for the entire system but only that sanctions deter crime. We take issue 

gives the one determining the crime rate, with this conclusion. We present detailed 

i.e., equation (5). In this system, however, it comments on these analyses, but first we is the variables W, X, and NW (the only mention a few key points relating to model 

socioeconomic variables included) that formulation and the statistical methods 

"identify" equation (5) and allow for the used: 

estimation of the key coefficients of the (a) Ehrlich assumed a priori the specifi- punishment variables, 61 and bz. Fisher cation of equation (3) thus leading him to 

and Nagin (1978) have noted that usiqg estimate a relationship that was linear in 

socioeconomic variables to identify simul- the logarithmic scale, i.e., equations (4) or taneous relationships can be hazardous. (5). He made no attempt to check the ap- We address this point below, but empha- propriateness of this assumption, or to 

size again that Ehrlich does not present his assess the overall goodness of fit of his 

entire system so it is impossible for anyone model. Many alternatives are available 

to completely judge his specification (see which are consistent with the original the related criticisms by Hoenack et al. econometric formulation. 

1978). (b) As noted above the use of the variEhrlich estimates the parameters in (5) for ables, W, X, and N W to identify the crime 

each of the seven basic crime types and for rate equation, (9, is highly suspect. 

various combinations of crime. Estimates (c) NO justification is given for the use of 

Wand X in place of the variables measuring the differential monetary returns of 

crime. 

(d) When fallible measures are used for 

key variables in a regression or simultaneous equation model, it does not suffice to 

substitute them directly into the model, as 

Ehrlich did with equation (3). The problems of dealing with models where there are 

errors in the variables are well-known (e.g., 

see Sprent 1969 or Zellner 1971). 

(e) There is a special statistical technology especially suitable to problems where 

there are multiple indicators available for 

given unobservable variables (see Joreskog 

1970 for a general formulation, and Bielby, 

Hauser, and Featherman 1977 for an illustrative application). Ehrlich simply ignores 

this matter. 

(f) The equations for all of the crimes include the monetary variables W and X, even those equations for violent crimes 

such as murder, assault, and rape. We see 

no justification for this. (Parenthetically, 

we note that Ehrlich classifies robbery as a 

property crime, whereas the FBI classifies 

it as a violent crime.) 

(g) The equations for each crime type 

are analyzed separately and not linked. In 

our view a more realistic model would relate crime rates to one another because of 

the known tendencies of career criminals to 

substitute one crime type for another (e.g., 

see Petersilia, Greenwood, and Lavin 

1978). 

Vandaele (1978) reanalyzed Ehrlich's 1960 

data, incorporating a number of different 

model specifications as well as an attempt 

to identify possible outliers, i.e., states 

whose data do not fit the pattern of the remainder. His analyses lead him to essentially the same conclusions as Ehrlich. We 

merely outline here some of the highlights 

of Vandaele's work. He supports Ehrlich's 

use of weighted least squares but notes that 

weighting the variables does not have any 

real effect on the conclusions. His analyses 

are also done in the logarithmic scale, 

although he does obtain one set of estimates for a model in which Q/ N is in the 

log scale and all other variables are untransformed. The results of this analysis 

are not very different from the others. Two 

different models for the supply-of-offenses 

equation that Vandaele fits include (a) the 

model of equation (9,where the reduced 

form contains only the 6 variables in this 

model together with (El N)59, and (b): 
Table 3. Estimated coefficients of In (C/Q)j and lnTj (from Vandaele (1978) 

Equation [51a Equation [51 Equation [5]C 

Offense In(CQ)j lnTj ln(CQ)j- lnTj In(CQ)j lnTi 

Murder p.492 -.124 -2.944 .I29 2.178 -.482 

(-.35)d (-.69) (-1.68) (.35) (.11) k.1I) 

Rape -.771 -.316 -1.347 -.699 -2.979 -1.240 

(-1.39) (-.78) (4.92) (-2.30) k.43) (v.38) 

Assault -3.882 -7.216 -.968 -1.412 3.851 5.754 

(7.35) (-.37) (-3.37) (-2.36) (22) L23) 


Robbery --4.223 -1.336 -1.584 ' -.465 -1.109 -.357 

k.57) (-.SO) (-6.49) (-1.46) (-2.19) (-1.24) 

Burglary -.445 -.793 -.884 -1.31 7 -.416 -.547 

(-2.73) (-2.99) (-6.05) (4.91) (-2.81) (-2.43) 

Larceny -1.441 -2.127 -1.554 -2.287 -1.231 -1.637 

(-1.63) (-1.93) (-1.65) (-1.52) 1 I ) (-1.58) 

Auto theft -.616 -.341 -.880 -.460 -.650 -.246 

(-2.58) (-1.66) (-3.65) (-1.76) (-3.22) (-1.25) 

All offenses 	 -1.021 -1 .I56 -1.249 -1.407 -1.043 -.824 

(-3.84) (-3.4) (-5.43) (4.30) (-3.70) (-2.57) 

a~odelidentified by the exclusion of In (k) 


59' 


b~odelidentified by the exclusion of In (k) and In (g) 59 59' 


'Model identified by the exclusion of In (i)59' 


d~umbers in parenthesis are t-ratios (i.e., the estimated coefficients divided by their 


estimated standard errors). 


where the reduced form includes only the Using the data reported in Vandaele's 

variables (6) together with (E/N)ss. The paper we have reestimated the parameters 

estimates of the coefficients of In Pand ln T for the equations determining murder and 

for these two models are given in Table 3, burglary. In both cases we were able to 

along with estimatesfor the model in which duplicate Vandaele's estimates up to roundthe crime rate equation is identical to (5), off error. For these two crimes our findings 

but where (Q/ N)59 is used as an additional agree with those of Vandaele in that the 

reduced form variable. Vandaele's overall burglary estimates are insensitive to 

conclusion is that the inferences about de- changes in specification while those for 

terrence are not sensitive to changes in the murder are not. We have done the analysis, 

specification of the model. A careful exam- in both cases, using a model that is linear in 

ination of Table 3 raises doubts about this the original scale and found that the results 

conclusion which we will return to later. are consistent with those for the logarithFinally, Vandaele notes that some states mic scale. The residual analysis (see, e.g., 

(Utah, Vermont, and Wisconsin) have re- Daniel and Wood 1972) indicates that 

corded values for some variables that are either of the models fits the data adequately. 

inconsistent, e.g., the estimate of C/Q, the We also agree with Vandaele's findings that 

probability of conviction for assault in deletion of the states with values of C/Q 

Vermont, is given as 1.56. These are not greater than 1 does not change the results, 

mistakes in recording but result from the but we do not agree that this is not a problem. 

way in which the variables such as ClQare 

defined (see Table 1). As we noted earlier Vandaele has stated that his conclusions 

the problems here include the lag between are not sensitive to changes in the specificaoffenses and imprisonments as well as tion of the model. This point is a crucial 

cross-overs between states. After redoing one since there is not nearly enough theothe analysis with certain of these states retical knowledge of the system to deteromitted, Vandaele claimed that the results mine which a priori assumptions are corare not substantially changed. He con-	 rect. Indeed many are likely to be incorrect. 

cludes that, although the question of what 	 Thus different estimates for the key coefis the proper model specification needs to 	 ficents corresponding to different specifibe studied further, the fact that the esti- 	 cations would force us to do more thinking 

mates do not depend on the specification 	 about the correct form. A careful examinalends support to the theory that sanctions 	 tion of Table 3 shows that, especially for 

are an effective deterrent. 	 the violent crimes of murder, rape, and 

assault, the estimates do change for the four 

specifications described above. Note also 

that there was some instability in the estimates for murder and assault. Thus we do 

not agree with Vandaele's claim. We see 

evidence of sensitivity of the conclusion to 

changes in the specification of the model, 

and given the comments of Fisher and 

Nagin (1978) concerning identification, 

this finding casts doubts on any inferences 

drawn. 

Continuing our analysis in a purely analytic framework, we note that multicollinearity is a serious problem in this data 

set. The correlation matrix indicates very 

high correlations am0r.g the socioeconomic 

variables. Our computations were done 

using a CDC 6600 computer and, although 

we did not run into any problems in calculating the inverses of matrices, it is well 

known that even a nearly singular design 

matrix can lead to unstable estimates of 

parameters. Another problem is that of 

"outliers" or what would be more appropriately called influential observations (see 

R. D. Cook 1977). These are points that 

are a large distance away from the "x-space" 

spanned by the other points. Vandaele just 

looked at univariate plots to determine if 

any outliers were present, but the use of 

univariate plots may be very misleading. 

Figure 1 shows a point which is clearly far 

from the others but the two univariate plots 

along the axes do not show this at all. An 

adaptation of Cook's techniques suitable 

for use in simultaneous equations problems would have been of great help in Vandaele's and our reanalyses. 

The most serious problem with Ehrlich's 

data and Vandaele's reanalyses of them, 

however, lies with the data themselves. We 

are trying to estimate effects of certain variables on others but we cannot observe what 

we desire. For instance, N Wis actually the 

percentage of blacks in the population, not 

the percentage of nonwhites. If this variable is attempting to measure minorities 

then it may be very misleading. We will see 

below in a reanalysis of 1970 data that 

changes in the way some of the variables 

are measured can yield very different results. Our biggest stumbling block is with 

Ehrlich's measure of the probability of conviction, one of the keys to the analysis. 

Since this measure is determined by the ratio 

of the number of convictions to the number 

of offenses, the "probability" may be larger 

than 1. While Vandaele minimizes this by 

showing that states with probabilities 

larger than 1 do not make a difference, he 

misses the point raised by the obviously 
w 

Figure1. 

Why one-dimensional graphs do 

not always indicate influential 

observations 

Y 

.. 

.. . . 

f -. 

G? 0 

m . v - X 

4 

wrong estimated probabilities. This variable is clearly not measuring (or at least not 

very well) what it is supposed to, and there 

is no way of determining whether a value 

of C/ Q equal to 0. l or to 0.2 is an accurate 

reflection of the probability of conviction 

in that state! We can all agree that an estimated probability of 1.6 is wrong because 

we know that probabilities cannot exceed 

one in value. When we observe estimated 

probabilities of conviction of 0.9 or 0.5 or 

0.3, however, what are we to do? Why 

should we trust the estimates of magnitude 

0.9 or 0.1 any more than we trust those of 

1.1 or 1.6? The problem may be that there 

are transitions between states which preclude using this measurement of the probability. At any rate, it seems impossible to 

justify seriously any inferences made using 

this measure of sanction, especially since 

Ehrlich uses ln(C/Q) in his equation rather 

than C/ Q. When C/Q is close to zero a 

small error in estimate is greatly magnified 

by taking logarithms. 

Forst S 1970 data 

Forst (1976) presents an analysis of 1970 

cross-sectional data that parallels that of 

Ehrlich. This analysis is based on data from 

all 50 states plus Washington, D.C. A 

description of 'the variables used is given in 

Table 4. Many of these variables are similar 

to Ehrlich's but there are some important 

differences. 

There are four variables that are measured 

differently in the two data sets: Forst measures the average length of prison sentence 

from the Statistical Abstract (1972) while 

Ehrlich uses National Prisoner Statistics; 

he uses YDSPR to measure income dispersion while Ehrlich uses the proportion of 

families earning below the median family 

income; he measures the proportion of 

persons between 18 and 20 years of age 

while Ehrlich uses the proportion between 

14 and 24; he measures population density 

from Census data while Ehrlich uses 

SMSA, the proportion living in standard 

metropolitan statistical areas. In addition, 

Forst uses four variables for which there 

are no corresponding measures in Ehrlich's 

analysis; namely MIGR, BRHO, QJ, and 

A VTMP. We will see below that the first 

two of these prove to be quite important. 

Forst models the criminal justice system 

using a five-equation structure: 

CR =fi(PJ, A VSENT, QJ, MIGR, 

URB, BRHO, MFY, YDSPR, 

UMPL, TEEN, MALE, 

N WITE, AUTEMP) 

PJ =h(POL$, CR, SOUTH, URB) (7) 

QJ =I;(Y/ POP, SOUTH) 

POL$ =fj(Y/ POP, CRl-I) 

COR$ =A(Y/ POP, CRt-I) 

where5 represents an affine function of the 

included variables. This formulation allows 

for transformations of variables such as 

PJ, which is a bounded dependent variable 

in the second equation. Two important distinctions between this model and Ehrlich's 

are that Forst considers police expenditure 

to be an exogenous variable (determined in 

this case by Y/ POP and CR I )and, more 

importantly, Forst uses considerably more 

variables to determine the crime rate. We 

also note that Forst analyzes only the 

aggregate crime rate, not the rates for 

individual crimes. 

Once again we will focus only upon the estimation of the crime rate, the first equation 

in (7). Forst presents his analysis with the 

variables measure in their original scale, 

i.e., the additive relationship as opposed to 

Table 4. Variables used in Forst's analysis 

the multiplicative one assumed by Ehrlich. 

He states that this is the more appropriate 

model because of the higher RZ (a comment which is incorrect statistically). 

Another point of difference is that Ehrlich 

assumed that the variance of the errors 

decreased with N, state population, and 

hence he performed weighted least squares 

with flas weights. Forst did not, empirically, find a need for such a weighting 

and hence did not use one. At any rate we 

will see later that the weighting does not 

have much of an effect on the conclusions. 

Forst's estimated coefficients are given in 

Table 5. These estimates imply conclusions 

very different from those of Ehrlich. Neither 

of the deterrence variables has significant 

coefficients and, in fact, the coefficient of 

A VSENT is positive. Note further that 

MIGR, URB, and BRHO appear to have 

strong effects on the crime rate. These three 

variables were not included in Ehrlich's 

analysis. Forst also replicated Ehrlich's 

analysis, as closely as possible, using the 

1970 data. He does not present specific results in his paper but notes that the estimated elasticities of the two deterrence 

variables are substantially smaller than 

Ehrlich's. It is difficult to judge how different things are since he provides no standard 

errors. It must be pointed out again that 

Forst provides no assessment of the fit of 

his model, aside from reporting RZ values. 

More will be said about this analysis as we 

present our analysis of this data set. 

The data set that we used in the analysis of 

the 1970 data was identical to that of Forst 

with the exception of three variables, 

Y/POP, YDSPR, and UMPL. We took 

Y/ POP to be "personal income"and these 

data were obtained from the Statistical AbC R 

PJ 

AVSENT 

QJ 

POL$ 

COR$ 

MlGR 

URB 

BRHO 

MFY 

Y(P0P 

YDSPR 

UMPL 

TEEN 

MALE 

NWITE 

AVTMP 

South 

: Number of FBI index crimes per 100,000 residents 

: Estimated probability of apprehension and imprisonment 

: Average time served by offenders 

: Expenditures on correction system per prisoner 

: Expenditure on police per state resident 

: Expenditure on correction system per state resident 

: Population migration rate (population growth divided by number of 

residents) 

: Proportion of residents living in places defined as "urban" by the Census 

Bureau 

: Proportion of households that are not husband-wife households 

: Median family income 

: Income per capita 

: Income dispersion (difference between median family income and national poverty level, weighted by proportion of families below poverty 

level) 

: Proportion of the adult population that is unemployed or not in the labor 

force 

: Proportion of residents between ages 18 and 20 

: Number of males divided by the number of females 

: Proportion of residents who are non-white 

: Average temperature (Fahrenheit) 

: Dummy variable distinguishing northern and southern states (south = 1) 

1 
I 

Table 5. Estimates of the crime-rate equation in [5] 

Forst analysis Our reanalysis 

-

Variable -Elasticity t-Ratio Elasticity t-Ratio Coefficienta 

PJ -.02 -.I4 .OO .O1 

AVSENT 31x10~ . .01 .10 -.oo -.oo QJ 46 x 1o-~ -.07 -.64 -.06. -.60 

MIGR -16 x 10-3 a 3.42 -.OO 3.70 

URB 

33 x 102 

.71 2.17 .74 2.40 

BRHO 26 x 102 

.96 2.13 .97 2.30 78 x lo2 

MFY .60 1.51 .57 1.50 15 x 10-2 

YDSPR .40 1.93 .33 1.80 

UMPL 13 x 10-1 

.ll .21 .20 1.90 98 x 102 

TEEN .63 1.45 .69 1.70 30 x 103 

MALE .65 .65 .43 .20 21 x102 

NWlTE -.07 -1.51 -.07 -1.70 -15 x 102 

AVTEMP .ll .37 .21 .70 9.3 x 101 

'Not computed by Forst. 

obtained are given in Table 6. The only significant variables in our analysis are MFY 

and YDSPR. Evidently the slight differences between Forst's variables and ours 

are giving very different results. The residual plots for this model, however, showed a 

definite need for fitting the additional 

variables, URB and MIGR, so we would 

not want to use the model, as it stood, for 

making inferences. 

Despite these discrepancies, our conclusion is the same as that of Forst: Usingvariables measured similar to those in his 

study, we find no evidence that, in 1970, 

sanctions were an effective deterrent to 

crime. 

stract (1975). In computing YDSPR we 

took the national poverty level to be$3,601 

as given in the Statistical Abstract (1975). 

The other discrepancy was for UMPL, 

which was supplied by Forst, but over average value differs from that given by Forst. 

Using the same model as Forst, we derived 

the estimated coefficients for thecrime rate 

equation given in Table 5. Our estimates 

are similar to Forst's with only that for the 

coefficient of UMPL being substantially 

different. Note that our estimate of the PJ 

coefficient is in fact positive although there 

is no strong evidence, in either case, of the 

actual coefficient being different from 0. 

Our analysis of the residuals from the fitted 

equation indicated that Michigan might be 

a possible outlier (it had a standardized 

residual of 2.6). Although testing this point 

as an outlier using a Bonferroni t-test (see 

Miller 1966) did not lead to rejection, we 

reestimated the parameters with this state 

omitted and found that they did not change 

substantially. Scatter plots of the variables 

indicated that the District of Coumbia (due 

to very high values of N WITE, BRHO, and 

POL$) and Alaska (with a very high percentage of males) were well away from the 

center of the array of independent 

variables. However, eliminating either or 

both of these points does not change the 

results either. One final point of note is that 

there was a tendency for the variance of the 

residuals to increase with URB. However, 

no heteroscedasticity was observed when 

the residuals were plotted against N. 

In Table 6 we give estimates for the coefficients when the model has all variables in 

logarithms and when only CR is in logarithms. Again the seemingly important 

variables remain the same. In both of these 

models there are no outlier problems nor is 

nonconstant variance apparent. Hence 

there is evidence that the logarithmic scale 

is the better one to work in, although the 

choice of scale doesn't affect the findings in 

a meaningful way. 

As mentioned above, Forst replicated Ehrlich's model as closely as possible and obtained results for 1970 data that were not 

consistent with Ehrlich's. We have also 

done this but our results do not agree with 

either Forst or Ehrlich. The estimates we 

Table 6. Estimated coefficients for various models fit to Forst data 

Variable Model (1 la Model (2) Model (3) 

h 

PJ 11 XIO-~ ( .42)b 2.2 ( .22) -.21 

AVSENT 3.7 x 10'~ ( .13) -1.9 x ( -30) -.I6 

QJ -3.9 x 10.~ ( -.20) -1.0 x lo-z ( -.77) - MlGR 80 x ( 3.33) 1.3 ( 3.17) -

URB 81 x10-~ ( 2.46) 1.4 ( 2.75) - BRHO 57 X lo-2 ( 1.12) 2.1 ( 1.31) - MFY 1.2 ( 2.67) 97 x lo-6 ( 2.11) 1.7 

YDSPR 62 x ( 2.95) 73 x ( 2.09) 1.O 

UMPL 31 XIO-~ ( 2.82) 4.9 ( 2.04) - TEEN 91 X ( 2.17) 20 ( 2.41) - MALE -2.0 ( -.91) -2.5 ( p.61) - NWlTE -6.9 x (-1.97) -.79 (-1.98) .04 

AVTEMP 33 X ( .92) 45 lo-5 ( .76) -

he three models used are: 

(1) All variables, except SOUTH, transformed to natural logarithms. 

(2) Only CR is transformed to natural logarithms. 

(3) This corresponds to Ehrlich's model using the 5 corresponding variables available in this data set. 

b~umbersin parentheses are t-ratios. 

The explanation for the discrepancy between Ehrlich's results for 1960and Forst's 

ones for 1970 may be simply that behavior 

patterns of criminals changed in these 10 

years. While certainly a possibility, this 

cannot reasonably be inferred from the 

data at hand. In comparing the two analyses, it must be remembered that the 1970 

data include only an overall crime rate and 

there has been no individual analysis for 

different crimes. Of course, we can compare the two results in terms of the overall 

crime rate but this may not be very fruitful 

as there are surely different structural relationships for different crime types which 

are masked by such an aggregation. 

Other analyses of cross-sectional data 

for murder 

Given the widespread interest in the potential deterrent effect of capital punishment 

on the commission of homicide, several investigators have done special analyses of 

cross-section data by state specifically for 

this crime. These include Passel1 (1975) 

who examines data for 1950 and 1960, 

Forst (1977) who analyzes data for 1960 

and 1970 (actually he used differences), 

Ehrlich (1977b) who uses data for 1940and 

1950 (his analysis of murder for 1960 was 

described earlier in this section), and Loftin 

(1980) who examined a quite different data 

set for 1960 which had been explored 

earlier by several sociologists. Because the 

longitudinal analyses described in the next 

section deal only with homicide, we defer a 

discussion of these cross-sectional studies 

until the end of that section. 
Deterrence, capital punishment, 

and murder 

Ehrlich S longitudinal data for murder 

One of the most controversial studies of 

deterrence is that of Ehrlich(1975a). Based 

upon a time series of aggregated national 

data for the years 1933-1969, Ehrlich 

claims to have found strong evidence that 

the death penalty has a deterrent effect 

upon potential murderers. In this section 

we review Ehrlich's analysis as well as 

prominent criticisms of it. We then present 

the results of our reanalysis of essentially 

the same data set. 

Ehrlich's model is one in which the murder 

rate, probability of apprehension, and 

probability of conviction given apprehen- 

;ion are -having 

simultaneous effects on each other over 

time, while a number of socioeconomic 

variables are considered to be exogenous 

variables along with the probability of execution given conviction. The murder 

supply function, by an elaboration of the 

earlier arguments, now replaces p* andf* 

of equation (2) by P, (the probability of 

arrest), P,I, (the probability of conviction 

given arrest), and PelL(the probability of 

execution given conviction). The empirical 

implementation of this function, using the 

variables described in Table 7, takes the, 

form: 

(i)P P- P P Pr = CP, IP.~:P~:U .L 

(8) 

x Y ,Ph AP7 exp (BxT) exp (4. 

Note that T (time) is entered into this 

equation in a manner different from all 

other variables. Time is used here as a surrogate for the improvement of medical 

technology over time and, as a variable, it 

plays a crucial role in the analysis, as we 

shall see below. 

Since the observations all involve aggregate national data measured annually for 

1933-1969, Ehrlich assumes that the errors are subject to first-order serial correlation, 

l.e., 

u1 = PUI- I + el, (9) 

where p is the serial correlation and the el 

are independent random errors. The equation whose coefficients he thus sets out to 

estimate is 

Table 7. Variables used in the time-series analyses 

-

Q 	 : Murder rate (per 1000 civilian population) N 

: Probability of arrest (percent of murders cleared) 

: Proportion of those charged that were convicted of murder 

: Number of executions for murder in the year t + 1 divided by the number of 

convictions in year t 

: Number of executions for murder in the year t divided by the number of 

convictions in year t 

L 	 : Proportion of the civilian population in the labor force 

U 	 : Proportion of the civilian labor force that is unemployed 

A 	 : Proportion of population in the age group 14-24 

: Friedman's estimate of (real) permanent-income per capita in dollars Y~ 

T : Time (years) 


NW : Proportion of non-whites 


N : Civilian population (in 1000's) 

XGOV : Per capita (real) expenditures (excluding national defense) of all governments 

in millions of dollars 

XPOCl 	 : Per capita (real) expenditures on police in dollars lagged one year 

: Violent crime rate (offenses of rape, robbery and aggravated assault) 

~l"($) 	 )' Po + BIAlnPd + P?A1np~]a 

+ PXAlnP,J, + p,AlnU 

+ Br AlnL + PsAln Y, 

+&AT+ e, 

where, for a generic variable Z, the value of 

AZ at time * is 

AZ = Z - ~ZI-I, 

and Po = 1nC. 

In a simultaneous equation framework, 

one must be concerned with whether or not 

the structural equations are identified. This 

particular equation is identified by omit: 

ting a number of socioeconomic variables 

from this equation. The variables that were 

omitted must have a direct effect on some 

of the other endogenous variables so that 

equation (10) can be identified, i.e., for the 

parameters to be distinguishable. Fisher 

and Nagin (1978) point out the difficulty 

inherent in using socioeconomic variables 

to identify the parameters in a structural 

equation. It is impossible to determine 

whether Ehrlich has validly identified his 

structural equations because he only presents the one equation given in (10). 

Ehrlich presents estimates of the parameters in equation (10) using six different 

measures of P,I,, the probability of execution given conviction. Two of these are defined in Table 7. In all but one of the six 

cases Pel, is viewed as an exogenous variable. He finds that for all six measures the 

estimated coefficient of the P,I, variable is 

negative. Also, for four of the six, the estimated coefficient is significantly different 

from zero (having a ratio smaller than -2). 

He also repeats the analysis after excluding 

some years from the beginning and some 

from the end of the series. These modifications do not change his resultsappreciably. 

Using two of the estimates, Ehrlich derives 

an estimate of the average number of murders that would be prevented by one additional execution per year. He estimates this 

to be between 7 and 8. 

Ehrlich concludes that his analyses show 

the deterrent effect of capital punishment. 

He claims that he has analyzed the data in 

scales other than the logarithmic one without the conclusions changing substantially, 

and he also states that his results are unaffected by the time period of analysis. We 

show below that there is considerable 

doubt about these two claims. 

Criticism of Ehrlich's conclusions can be 

divided into two broad categories: the relevance and accuracy of the data sources, and 

the methodology used. We address these in 

turn. The reliability of the data sources that 

Ehrlich used has been questioned before. 

We noted earlier the severe shortcomings 

of the UCR crime rates. They are not 

accurate measures of the variables that 

they claim to represent. Furthermore, 

Bowers and Pierce (1975) point out that the 

UCR arrest and clearance rates are especially suspect, primarily in the earlier years. 

What is particularly troublesome is that 

recording practices have changed so much over time. Moreover, while the UCR 

murder rates have been reestimated for the 

earlier years, the arrest and clearance rates 

have not been so adjusted. When one is 

making inferences based upon a time series, 

such dramatic changes in the coverage of 

data collection inevitably are confounded 

with any real effects that are present. 

A second data-related problem is conceptual as well. The variable Pelc relates to 

crimes of murder subject to punishment by 

execution, actually a small proportion of 
- - - - - - - - - 

Table 8. Comparison of estimated coefficients in equation [lo] 

A 

P Constant 'a Pcia PXQl U L Y~ A T 

Ehrlich's 

estimates 

a) .257 -3.1 76 -1.553 -.455 -.039 .067 -1.336 1.481 .630 p.047 

( -.78) (-1.99) (-3.58) (-1.59) (2.00) (-1.36) (4.23) (2.10) (-4.60) I I 


Our 


estimatesa 


b) .257 -2.02 -.56 u.25 -.038 .01 -.91 .65 .71 -.02 


(-2.61) ( -.55) (-1.57) (-1.24) ( .26) ( I (2.64) (2.28) (-2.6) 


"our estimate of p was actually $=.55 but we present estimates using the same value as Ehrlich obtained for comparison purposes. 

Our estimates were not sensitive + changes in p except for p near 1. 

all murders and one which varies from state 

to state. Yet the UCR data used by Ehrlich 

for the number of murders, the number of 

arrests, and the number of convictions 

refer to all murders and nonnegligent 

homicides rather than to only capital 

crimes. If both capital and noncapital murder rates have production functions of the 

form (8), then the overall murder rate can- not have a production function of this form 

(see the related discussion in Hoenack and 

Weiler 1977). Ehrlich's discussion of this 

problem is noninformative and sidesteps 

the issues. 

The data used for PC],present further problems. particular, the data for P,,d and 

XPOL were not available for odd years 

from 1913-1951. Ehrlich estimated these 

values by a regression technique that he 

does not describe. Among the many prob- lems inherent in this type of procedure is 

the loss in real degrees of freedom due to 

the missing data. The effective degrees of 

freedom for estimation is an important 

issue here and more will be said about it 

later. 

A fourth problem that ~-,~li~h faced was

that there were no executions after 1967. 

He arbitrarily defined the number of executions in those years to be one in order to be 

able to take logarithms. This is indicative 

of a basic flaw in the production function 

model of equation (8). ~t is simply inapprofor application to a social structure 

allowing zero executions, since it predicts 

an essentially infinite murder rate for such 

situations if the coefficient pl is negative 

(i.e., the sign associated with a deterrent 

effect of capital punishment). 

An overriding issue related to the data is 

the choice of aggregate data for making Inferences. Baldus and Cole (1975) include an 

excellent discussion of the dangers of 

making causal inferences using nationwide 

crime data. They note that crime patterns 

have differed over time from state to state as has the use of the death penalty. If murder rates increased in states that used the 

death penalty often, but rates decreased in 

states not using the death penalty, the use 

of nationwide data might completely obscure this fact. 

Assuming that the variables used in the 

study are faithful measures of what we 

really want to observe (which we believe to 

be untrue), there are still a number of methodological questions to be answered. 

Ehrlich's model is linear in the logarithmic 

scale (although he leaves Tuntransformed) 

and a number of authors have shown that 

the conclusions reached are dependent 

upon the scale of measurement. Passel1 and 

Taylor (1977) and Bowers and Pierce 

(1975), using data sets that are effectively 

identical to Ehrlich's, find that the coefficient of PC(,is not significantly different 

from zero when estimated in a model that is 

linear in the original scale of measurement. 

Finally, we note that all of the variables 

actually used by Ehrlich are fallible meas- ures of the variables of interest, and that 

the models of real interest should thus invalve errors-in-the-variables, and multipleindicator structures. ~h~ difficulties here 

are the same as those described in the last 

section. 

Another methodological question is whether 

the relationship between theactual variables 

used is changing over time. Passel1 and 

Taylor and Bowers and Pierce indicate that 

the data for Years after 1963 exert heavy influence on the estimated coefficients. In 

their analyses, both sets of authors show 

that the effect of Pel,is not significant when 

these later Years are deleted from the data 

set (see the related discussion in Klein, 

Forst, and Filatov (1978)). Passell and 

perform an F-test determine if 

the regression function is the same for the 

years before 1963as for the years after 1963 

and conclude that it is not. (Unfortunately, 

as Ehrlich (1977a) notes, the properties of 

their test statistic are not known.) Further, 

Bowers and Pierce argue that doing the 

analysis in the logarithmic scale gives more 

weight to these later years. In his rebuttal to 

Bowers and Pierce, Ehrlich (1975b) claims 

that there is no justification for arbitrarily 

deleting data points and that doing so loses 

precious degrees of freedom. While there is 

some validity to Ehrlich's response, the 

deletion of these points is not arbitrary if a 

fundamental change in American society took place around 1963, as has been argued 

by many criminologists and sociologists. 

Moreover, as we found in our reanalyses 

described below, these years stand out as 

discrepant in various forms of residual 

analysis. 

K1ein, Forst, and Filatov a 

number of 

that Ehrlich might have used. One is the 

average length time served by 

murderers-it very well may be that this is 

the for explaining the 

increase in murders. lhese 

data are not available. Another 

variable that they do use is an overall index 

of violent crime. The justification for its inelusion is that murder may be increasing as 

a by-product of an overall increase in the 

level of lawlessness. Reanalyzing Ehrlich's 

data, they find that with this extra variable 

in the structural equation the coefficient of 

Pel,is no longer significantly different from 

zero. 

Hoenack and Weiler (1977) reanalyzed the 

Bowers-Pierce data, using a fully specified 

simultaneous system of equations, a theoretical justification for which is given in 

Hoenack, Kudrle, and Sjoquist (1978). 

Their model interprets Ehrlich's murder 

supply function as the society's response to 

murder behavior, not vice versa. For their 

specification, the coefficient of the execu- tion variable is positive although never 

more than one standard deviation from 

zero. A key feature of their specification is 

the of the the proportion of the population between the ages 

of 14 and 24, into two parts: one for the 

proportion of juveniles (ages 14-18) and 

One for young (ages 19-24). We 

"Ote that their require the inclusion of T(its estimated coefficient is essentially zero when included); this 

point is especially interesting given the crucia1 role played by Tin Ehrlich's analysis 

and specification, which we discuss in 

detail shortly. 
These criticisms raise a number of questions. The estimated coefficients differ depending on the scale in which theanalysis is 

done, but which is the proper scale? The 

estimates are affected by the later years 

(1963-1969) but what distinguishes these 

later years from the earlier ones? A further 

criticism deals with the basic formulation 

of the model as a simultaneous set of equations and the identification of the key structural equation for the supply of murders. 

We use a somewhat different approach in 

our analysis and try to answer some of 

these and other questions. 

In our analyses we have used data furnished 

by Bowers and Pierce and used in their 

analyses. Ehrlich consistently refused to 

make his data available to us and to others 

for reanalysis. The only versions of the 

variable Pel, that we had values for were 

PXQl and PXQ2. The bulk of our analysis 

focused on using either PXQl or its lagged 

values, PXQlI-I], as a measure of probability of execution given conviction. 

Our first goal was to see if we could reproduce Ehrlich's results using this data set. In 

Table 8 we give our estimates, along with 

Ehrlich's, of the coefficients in the murder 

rate equation. Note that the signs of all coefficients agree but that there are some differences. The likely cause of the different 

estimates is in Ehrlich's estimation procedure based on the method of Fair (1970). 

We have programmed a method suggested 

by Fair ourselves to get estimates, while 

Ehrlich used a packaged routine. We suspect the problem is in how the modified 

first differences are created. Fair actually 

suggests a number of different methods, 

some of which are asymptotically more 

efficient than thers. The method that we 

adopted uses (8,-pPI=l)as the values for 

the endogenous variables in the second 

stage regression. Thus in our analysis the 

effective years are from 1934-1969. Ehrlich 

appears to have used a somewhat different 

differencing operation which allowed an 

analysis only for the period 1935-1969. At 

any rate, the conclusions based upon our 

estimates are not substantially different 

from Ehrlich's. A ' major discrepancy 

occurs in the estimates of b. We found a = 0.55 while Ehrlich reports a =0.257. Since 

our estimates were not very sensitive to 

changes in 0 (except near 1) we used 

Ehrlich's value to get the remaining 

estimates. 

We take issue with Ehrlich's arguments for 

the endogenous variables Q/ N, P.,, and P,I, 

having simultaneous effects on one another. 

It makes far more sense to us to think of a 

criminal's subjective assessment of punishment rates as affecting his current behavior, 

but that the murder rate affects the punishment variables after some delay of time. 

The delay might be 6 months, 1 year or 

even 2; however, since the data only allow 

for delays which are multiples of a year, we 

have arbitrarily fixed on a delayed effect of 

murder rates on punishment of 1 year. This 

assumption means that our system of equations, unlike Ehrlich's, is recursive not simultaneous, and thus we do not have 

Ehrlich's identification problem nor the 

problem of making inferences about structural parameters. Our model differs in this 

way from those used byLEhrlich, Bowers 

and Pierce, and Passel1 and Taylor, and we 

use it primarily to make a series of methodological points. 

Our model for reanalysis is thus of the 

form: 

where the errors, e,,are assumed to be,independent with mean 0 and variance a;(i.e., 

independent for different points within 

equations). A subscript of (-1) indicates 

that the variable was lagged by 1 year. By 

assuming that the errors are independent 

for different points within equations, we 

have set p = 0. This zero value for the serial 

correlation is completely consistent with 

our findings in the replication of Ehrlich's 

Figure 2. 

Residual plot for the crime rate 

equation in [I 21 

.10-,69 


a68 


.05... @67 
 - . .... . J ... ..

. . 

results, greatly simplifies the estimation, 

and allows for detailed residual analyses 

based on standard methods for multiple 

linear regression. Those residual plots that 

we have examined indicate that this 

assumption may not quite be met, but 

when we have reestimated the parameters 

assuming different values for the firstorder serial correlation coefficient we have 

found that the estimates do not change 

substantially. The residual plots indicated 

that the correlation might be of greater 

than first order but this possibility was not 

explored. If such higher order serial 

correlation exists, it affects Ehrlich's 

analyses as well as our own. 

Table 9 gives estimates of the coefficients in 

the murder rate equation for different 

transformations. Note that the first two 

sets of estimates are for an equation that 

does not include C, the violent crime level 

index. We considered three different measures of PC(,: PXQI, PXQI 1-11, and PXQ2. 

The only significant coefficients (whose 

t-values, which are given in parentheses, are 

in excess of 2) are for PXQi when variables 

are measured in the original scale or when 

only Q/ N is measured in the logarithmic 

scale. These equations are the only ones to 

contain significant coefficients for the 

other punishment variables, namely P,I,. 

Bowers and Pierce (1975) conclude that 

Ehrlich's results are heavily dependent on 

the analysis being done in the logarithmic 

scale. They state that due to the very low 

number of executions after 1962, taking 

logarithms of PXQl emphasizes the effect 

of these later years thus yielding a negative 

coefficient which is significantly different 

from zero. Our conclusion, after studying 

the residual plot shown in Figure 2 as well 

as other graphs, is in conflict with theirs. 

Taking the logarithms of PXQl moves the 

values of PXQIin later years far from the 

center and tends to flatten out the slope. 

These residual plots do, however, support 

the conclusions of Bowers and Pierce and 

of Passell and Taylor that the years after 

1962 do not fit the pattern of the previous 

ones. 

Other residual plots that we examined indicated a second problem which has not 

been noted in previous analyses. Large 

residual values corresponding to 1934 

point to it as a possible outlier. Looking at 

the original data, we find that for 1934 

there is a very large value of PXQl and a 

small value of Q/ N. We suspected that this 

point might have a strong effect on the estimates so we reestimated the coefficients in 0 0 :----.--

.. . . 2 both the original and the logarithmic scale. 

-:05 

64 63 062 


-15: ; k a a : ! : : + 


-4 -2 0 2 3 


LnPXQ, 


i . 

Table 9. Estimated coefficients for equation [ I 21 under various transformations 1 	 1 


PXQ, 

-

Pa 

1b - -.99 

(-1.16 

gb 	 -1 .0x104 

k.38) 

2P PXQ~ ---- L u A Y~ -T c 

.I4 .063 -64 -. 084 .81 w.029 -.13 .39 

(1.00) (1.91) (7.49) (-1.83) (3.00) k.09) (-.93) (1.95) 

-1 .8x104 -7.6x10-~ -.20 4.0x10-~ .035 1.1 xlw5 -.002 9x10.~ 

(-1.5) (-1.04) (-3.33) (-2.35) (.78) (1.31) (-7.62) (9.00) 

aTransforrnations are designated as follows: 

1. All variables in logarithms, 

2. All variables except T in logarithms, 

1 3. All variables untransformed. 4. in logarithms, all others u.transformed. 

b~hedata for 1934 were deleted in estimating the coefficients. 

These estimates, given in Table 9, show 

that things do change considerably once 

1934 is deleted. The estimated coefficient in 

the original scale is still negative but not 

significant while the estimate in the logarithmic scale is now positive. The residual 

plots after deletion of this point do not 

indicate any other outlier problems. We 

note that in Ehrlich's analyses, a significant 

result is obtained when using PXQI but 

not with PXQI.With the lagged variable, 

PXQl (- I,,the value for 1934 is used while 

for PXQl that year's data are excluded 

from the analysis. This seems to support 

our finding regarding the suspect nature of 

the 1934 data. 

It is not surprising that one point can exert 

such a strong effect on the estimated coefficients. Even in our recursive model there 

are only 25 degrees of freedom available for 

estimating the coefficients in the model. In 

Ehrlich's model the problem is much 

worse. Although Ehrlich, as well as other 

authors, have routinely computed the 

degrees of freedom associated with their 

estimates, it is not clear what the effective 

degrees of freedom actually are in a twostage estimation problem. In Ehrlich's first 

stage regression, there are 18 independent 

variables in addition to the 9 independent 

variables in the second stage regression. As 

far as we know, there has been no work 

done on determining the appropriate 

degrees of freedom for this type of problem 

but we would think there are considerably 

fewer than 25. The difficulty in computing 

degrees of freedom is compounded by 

Ehrlich's estimation of the missing values 

of P,[,and XPOL using the remainingdata. 

Table 9 contains only the results for equation (12) of our three-equation model. We 

have analyzed the other equations as well 

but do not report on them-here since they 

do not affect the deterrence hypothesis. 

Earlier we noted the arbitrary choice by 

Ehrlich of the use of logarithms for all variables but T, time. In Table 9 we show some 

equations where in T was used in place of T 

in a fully logarithmic specification. The 

changes in sign for the coefficient of PXQ 

that go with this change in specification are 

suggestive that the choice of scale for the 

variable T may have a strong influence on 

the coefficient. Now the arbitariness of 

Ehrlich's choice hits home. Why choose T 

or log Tinstead of TI, or In(T- 1900), or 

even In(T - 1776)? In other reanalyses we 

have discovered that suitable transformations of Tcan dramatically change the size 

and sign of the coefficient of PXQl. 

In summary, we find that these data do not 

support Ehrlich's conclusion that there is a 

deterrent effect created by an increase in 

the probability of execution. First, we find 

the model formulation suspect, and inappropriate for application in-situations with 

essentiallv zero execution rates. Second. 

we the choice of data used td 

measure key variables in the model. Third, 

we have noted that the analysis is sensitive to 

the specification of the model. Using a 

recursive model we have obtained results 

that are different from Ehrlich's. The ques- 
tion of which model is more appropriate is 

not an easy question to answer, but we 

think that there is as much apriorisupport 

for our model as for Ehrlich's. Our residual 

analysis does not indicate any lack of fit 

other than the two problems discussed 

above; in contrast Ehrlich does not 

examine the goodness of fit of his model. 

Others, such as Bowers and Pierce (1975) 

and Hoenack and Weiler (1977), have also 

formulated alternative model specifications 

which when used in analyses make the 

deterrent effect of capital punishment disappear. In all, there are far too many flaws 

in Ehrlich's model, his data, and his analyses for him to claim that a real deterrent 

effect of any sort has been found using this 

form of longitudinal data. 

Cross-section analyses of murder rates 

To buttress the arguments in his paper on 

the analysis of the longitudinal data on 

murder, Ehrlich (1977a) has also analyzed 

the cross-sectional variations of murder 

and execution in 1940 and 1950. The basic 

regression model used in his analyse~ 

resembles equations (4), (9, and (10). 

Ehrlich uses ordinary least squares to estimate the coefficients in equation (15) and 

uses data first for states with positive executions, and then for all states. He also 

attempts to compare the results of a fully 

linear specification with (15), using an 

approach suggested by the method of Box 

and Cox (1964). His comparison strongly 

favors the log-log specification of (15). 

Ehrlich finds the estimated coefficients of 

T*, Q/ C, and PXQ (measured in several 

different ways) to be negative and significant at at least the 0.05 level both for the 

linear and log-log specifications. His conclusion is that these data and the analyses 

of them corroborate his earlier analysis of 

the longitudinal data. 

As in Ehrlich (1975a) these conclusions 

seem at first sight convincing, until we note 

that the data used have even greater shortcomings than those noted earlier and that 

almost all of the other analytical problems 

mentioned earlier remain. Moreover, Ehrlich's results run contrary to those of other 

investigators who have examined crosssectional data. For example, Passe11 (1975) 

used 1950 and 1960 data to estimate thecoefficients in the model, 

where Iis the percentage of the family population below an arbitrary cash income 

poverty line, and M is the ratio of net nonwhite migrants in the previous 10 years to 

the total population. Using both ordinary 

and two-stage least squares he found positive (but not significant) estimated coefficients for PQX, and negative (and significant) estimated coefficients for C/ Q and 

T*. Passell's specifiction, unfortunately, 

has little more to recommend it than does 

Ehrlich's, but his results do illustrate the 

importance of the specification on the results and the inferences one is likely to draw 

from the analysis. 

Forst (1977) examined data on the change 

in the crime and punishment measures that 

occurred between 1960 and 1970 for all 50 

states. In regressions based on a subset of 

32 states for which complete data were 

available, he found the execution variable 

to have a positive coefficient. Although his 

results appear to be in agreement with 

Passell, they are almost certainly dominated by the fact that PXQ for 1970 for all 

states was zero! Forst models the change in 

the homicide rate, A(Q/ N), as a function of 

the change in execution rates, A(PXQ), 

and changes in other variables. Since 

PXQ = 0 for all states in 1970, Forst thus 

models A(Q/ N) as a function of PXQ for 

1960 and the changes in other variables. 

We do not understand the logic behind this 

specification. 

Finally we note the analyses carried out by 

Loftin (1980) for 1960 cross-sectional data 

using a markedly different set of variables 

aside from C/Q and T*, motivated primarily by sociological rather than economic 

considerations. Loftin finds little to support the inclusion of the punishment variables in a regression equation with either a 

linear or a log-log specification. 

We have concluded that these crosssectional analyses offer no support to the 

conclusion that there is a deterrent effect of 

capital punishment, and the conflicting 

results for the other punishment variables 

cast serious doubt on any attempt to infer 

deterrent effects. 

Conclusions 

Becker's (1968) paper has stimulated many 

economists and others to use modern statistical methods for the analysis of regression and simultaneous equations models to 

search for evidence in support of the deterrence hypothesis. Following Ehrlich's 

(1973a, 1975a) pioneering attempts to implement Becker's theoretical model, the 

flood of papers and manuscripts on the 

analysis of crime and punishment data has 

been almost overwhelming. 

What has this work contributed to our 

knowledge of the deterrent effects of punishment on crime? We have concluded that 

little or no progress has been made during 

the past 10 years in our understanding of 

the potential deterrent effects of punishment on crime. Indeed much of the controversy that erupted over Ehrlich's work has 

served to divert the efforts of serious 

scholars of crime from more productive 

pursuits to a battle with Ehrlich and his 

supporters. The battle has raged before the 

United States Supreme Court, which heard 

arguments based on Ehrlich (1975a) and 

Passel1 and Taylor (1977) in the case of 

Fowler v. North Carolina. It has filled the 

pages of many different journals. Some 

journals devote entire issues to the topic 

(e.g., see Journal of Behavioral Economics, 

Vol. 6, Numbers 1 and 2, Summer/ Winter, 

1977). It has been investigated by a panel 

established by the National Academy of 

Sciences. And in the end we seem to be no 

further ahead of where we were 10 years or 

more ago. 

In this paper, we have reviewed a large proportion of the empirical attempts to model 

the economics of crime and punishment, 

including the work of Ehrlich (1973a, 

1975a) based on the model suggested by 

Becker (1968). We have concluded that: 

(a) The Becker-Ehrlich model has glaring shortcomings and, when examined critically, does not lead to the claimed testable 

hypotheses regarding the effect of punishment of crime. 

(b) The use of the Becker-Ehrlich model 

for aggregate data requires extensive justification that has never been given. 

(c) The crime and imprisonment data 

used to empirically examine the BeckerEhrlich model are so untrustworthy as to 

render any serious analysis meaningless. 

(d) The empirical implementations of 

the Becker-Ehrlich model are badly flawed 

and have extremely grave statistical shortcomings, and most published conclusions 

from them are not to be trusted. 

(e) Even if one accepts the BeckerEhrlich model, and Ehrlich's choice of data 

to implement it (which we do not), Ehrlichf 

affirmative conclusions regarding the deterrent effect of punishment on crime in 

general, and of capital punishment on murder in particular, do not stand up to careful 

statistical scrutiny. 
Ehrlich's critique of the National Academy 

of Sciences Panel's report (Ehrlich and 

Marks 1978) is essentially an attempt at 

self-justification. He argues that only his 

version of the econometric model of deterrence is relevant, that any work inconsistent 

with it can be dismissed out of hand, that 

only analyses done by Ehrlich (or those 

confirming his findings) are correct or appropriate, and that all of the work of others 

whose conclusions run counter to Ehrlich's 

is incorrect, distorted, technically flawed, 

theoretically eclectical, or irrelevant. This 

is hardly a dispassionate perspective, and 

we find little in the critique which counters 

the crucial points made in the preceding 

sections and in the Panel's report itself. 

We find no reliable empirical support in the 

existing econometrics literature either for 

or against the deterrence hypothesis. 

Moreover, we believe that little will come 

from further attempts to model the effects 

of punishment on crime using the type of 

data we have described in this paper. 

Acknowledgments 

The authors are indebted to several of the participants of the SSRC-LEAA Workshop whose 

ideas and ?suggestions inevitably have found 

their way into this article, although perhaps in a 

distorted way. In particular, thanks are due to 

Albert D. Biderman, Alfred Blumstein, William 

Fairley, Kinley Larntz, Colin Loftin, Daniel 

Nagin, Albert J. Reiss Jr., David Seidman, and 

Leslie Wilkins. We also wish to thank the many 

others who have shared their thoughtsand work 

with us, including William Bowers, Phillip 

Cook, Franklin Fisher, Brian Forst, Stephen 

Hoenack, Paul Meier, Frederick Mosteller, 

Glenn Pierce, Christopher Sims, Walter Vandaele, 

Ann Witte, and William Weiler. William 

Bowers, Brian Forst, and Walter Vandaele all 

provided their data for our reanalyses; lsaac 

Ehrlich consistently refused to make his data 

available. 

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Criminaljwtice planning 


A prolegomenon for a macro model 

for criminal justice planning: 

JUSSIM Ill 

ALFRED BLUMSTEIN 

Urban Systems Institute 

Carnegie- Mellon University 

GARYC. KOCH 

Department of Biostatistics 

University of North Carolina 

JUSSIM I is a deterministic, steady-state, 

nonqueueing flow simulation of a multistage system like the criminal justice 

system. The flow is processed through 

stages, and the process is characterized by 

an input into the first stage and by stage-tostage branching ratios. At each stage, 

resources are applied to the units of flow, 

resulting in linear costs and resource consumption. JUSSIM I1 expands on JUSSIM 

I by incorporating the feedback flow of 

recidivists through subsequent arrests. In 

this paper, an expanded "JUSSIM 111" is 

outlined. JUSSIM 111 incorporates a 

crime-generation process and a victimgeneration process from the characteristics 

of offenders and victims. Offenses are generated by first-time offenders coming from 

the general population and recidivists released by the criminal justice system. Similarly, the population produces first-time 

victims from a potential victim population, 

and "victim recidivism" provides an opportunity for further victimization, which 

could be influenced by the victim's selfprotective actions. The offense and victimization processes interact in a "victimization events" stage. The paper considers the 

various sources of data which could be 

used to generate the parameters of such a 

model and the statistical approaches to 

identifying the important parameters and 

for developing estimates for them. 

I. Background and need, 

for the model 

The principal computerized model in current use in the criminal justice planning 

process is the JUSSIM I model (see Belkin 

et al. 1971) which examines the "downstream" flow through the criminal justice 

system beginning with crimes and following the handling of such crimes as they 

become associated with suspects, defendants, convicted offenders, and prisoners. 

JUSSIM I1 (see Belkin et al. 1974) incorporates recidivism into that model through 

the addition of the feedback features 

associated with re-arrests. These features 

include probability of re-arrest at various 

points of departure from the criminal justice system, the time lags until recidivism, a 

crime-type-switch process reflecting the 

transformation from a previous crime type 

to a subsequent crime type, and a distinction between virgin arrestees (those arrested for the first time) and recidivist 

arrestees. 

The JUSSIM I model has seen fairly 

widespread implementation (as discussed 

in Cohen et al. 1973 and Blumstein 1975), 

but very little actual use has yet been made 

of the JUSSIM I1 model. This is true 

largely because of the limited availability of 

data on recidivism, and to a lesser degree, 

because the intelligent use of this more 

complex and advanced model demands 

greater technical sophistication. JUSSIM 

I1 is, however, now ready for implementation in a number of jurisdications, and so it 

is important to begin consideration of the 

future generation of such planning models. 

In this paper, we expand the view of the 

existing JUSSIM models to introduce the 

following additional considerations: 

(1) Explicit concern for the demographic and socioeconomic characteristics of the 

population generating criminality. 

(2) Explicit concern for the demographic and socioeconomic characteristics of the 

population generating victims. 

(3) Explicit concern for the effect of the 

criminal justice system on crime reduction 

through incapacitation and deterrence. 

(4) The effects on crime of environmental factors such as the state of the economy 

or social conditions. 

Even though the information on most of 

these relationships is still extremely limited, 

there are nevertheless im~ortant reasons 

for pursuing the development of a model 

that incorporates them. Such a model 

forces an identification of the relevant variables in those relationships, and so iterates 

with the data collection process to assure 

that the information to be collected is consistent with the formulation of that model. 

Alternatively, as the data arrive from the 
I

Figure 1. 

Total v~ctimizations 1 

w w 

a Trial

Switch 

matrix 

Potential 

offender 

copulation 

Slk 

)r 

Non-reports 

Conviction 

Release 

I' Virgin 

Offenders Victimization 

events 5 Milk 

Compensatlonf 

restltutlon 

Precaution J 

Recidivists 

Offender 

reaction 

1 Institution 1-4 community 1 1 

Non-arrests 

b

* 

Arrests 

I Dlsmlssed 

various data collection programs, they pro- The need for developing models is particuvide a stimulus for reshaping the formula- larly important today in view of the major 

tion of the model. This interaction between data collection efforts being undertaken. 

the data and the model represents an These include: 

important contribution of any such model (1) The Offender-Based Transaction 

formulation. Statistics (OBTS) system, which tracks 

individual crimes and arrestees in their 

processing through the criminal justice 

system. 

(2) The National Crime Panel's victimization survey, which collects a wide vari-

(3) The increasingly computerized criminalhistory records (or "rap sheets") such as 

the FBI's Computerized Criminal History 

(CCH) file which records for each individual the sequence of his arrests and 

any relevant dispositional information that 

subsequently becomes available for each 

arrest. 

In addition, a variety of computerized systems are being developed for handling the 

specific functions of various subsystems of 

the CJS. For example, the PROMIS 

system, designed to aid prosecutors, 

maintains detailed information on defendants as they are handled through the 

prosecutory processes. 

1 

All of these data systems were devised and 

are used for reasons other than the 

formulation and use of a planning model, 

and most of them are relatively unresponsive to the information demands of such a 

model. Nevertheless, the data they do pro-

-

vide can often be transformed into appropriate inputs for a planning model. In 

addition, the planning model can indicate 

variables central to planning but for which 

no appropriate data collection system has 

yet been organized. Those variables, once 

identified, might then be appended to existVlct~m 

reactlon 

ing collection efforts or, in some cases, 

might warrant an entirely new data 

collection effort. 

Even though the principal value of such a. 

model at this time is in shaping data collection and manipulation and in the formulation of functional relationships, it could 

ultimately. become an important policy 

instrument when it is developed and 

provided with appropriate and valid data. 

That role, however, will continue to be 

limited by the validity of the assumed relationships incorporated into the model. As 

the forms of those relationshipsare revised, 

further modifications of the models will 

become necessary.

1 II. Basic structure of the model 

/ A. Flow diagram. The basic structure of 

the model is shown in Figure I, which 

depicts the flow of virgin offenders from a 

"criminal population" and of virgin victims 

from a "victim population" (both of which, 

of course, are drawn from the same total 

population) into a "victimization events" 

stage where the offender and the victim 

interact with each other or with other recidivist victims and/or offenders in the 

ety of personal and crimeexperience data 

from a sample of householdsand businesses. 
generation of victimization events. Subsequent to that victimization, the event is 

either reported or unreported and, if reported, an offender may or may not be 

arrested. If arrest occurs, then the suspect is 

handled through the criminal justice 

system; he may be dropped out at any one 

of a number of stages of successive penetration through the system; and then he may 

either recidivate or desist from future 

criminal activity. 

The victimization process has a similar 

"recidivism" loop in which a victim may 

subsequently engage in various forms of 

preventive action reducing his vulnerability 

to victimization, and he may or may not 

subsequently become a victim again. In 

both the offender and the victimization 

recidivism processes, there is a "crimeswitch" process reflecting the possibility 

that a subsequent appearance involves a 

different crime type than the previous 

appearance. 

This structure deals with all the functional 

aspects explicitly incorporated into the 

JUSSIM I and JUSSIM I1 models, 

particularly the considerations of flow, 

resource consumption, and CJS workloads 

associated with JUSSIM Iand the rehabilitationlrecidivism aspects of JUSSIM 11. In 

addition, however, it introduces a number 

of new considerations. First, it goes back 

from the crime or arrest stage to identify 

the relevant criminal population and the 

relevant victim population in terms of their 

demographic and socioeconomic characteristics. In addition, it incorporates the 

effects of the various "environmental 

factors" (e.g., economic conditions, social 

conditions) as considerations in their criminality or victimizationvulnerability. Otherwise, the model attempts to reflect the 

deterrent effects of actions within the 

criminal justice system on the criminality 

of the relevant potential criminal population as well on the recidivism characteristics. The following discussion of each of 

these aspects of the model indicates how 

these representations would be accomplished. 

B. Identification of parameter groups. In 

this section, the major groups of variables 

are identified, and their individual structures, their relationships to each other, and 

the effects of exogenous variables are 

explored. 

(I) Potential offender population (si~). 

The potential offender population is 

created by exhaustively partitioning the 

total population (a)into subpopulations 

indexed by a subscript i=1,2, . . . ,NO.The 

partitioning is based on demographic variables such as age, race, sex, and marital 

status, as well as socioeconomic variables 

such as education, income, and employment status. The partitioning is intended to 

divide the total population intosubpopulations which have reasonably homogeneous 

crime-propensity rates (t,~) which can then 

be measured for each crime type, k. 

(2) Victim population (V,r). Similarly, 

the total population is partitioned into victim subpopulations which are indexed by 

subscriptsj = 1, 2, . . . ,Nv. This partition is 

likely to be different from the partition into 

which the offender population was structured, for it represents groups with internally homogeneous victimization risks. 

This might reflect their "value" as victims 

of crime as well as their vulnerability to 

potential offenders. The strycture might 

include business or commercial enterprises 

as well as individuals. Here also, a victimization rate (g,~) would reflect the rate at 

which a member of the j'h victim subpopulation becomes a victim of crime type k. 

(3) Victimization events (M,,L).The central feature of the model is the stage labeled 

"victimization events." This stage involves 

the convergence,of the offenders who come 

initially from the "potential offenders" 

population and the victims who come initially from the "potential victims" population. Both of these "potential" populations 

first generate first-time or "virgin" offenders and virgin victims, many of whom 

reappear subsequently as recidivist offenders and recidivist victims. A victimization event involves the joint interaction of 

an offender of type i with a victim of type j 

in a crime of type k, and so the victimization events are characterized by rate 

parameters M,,r, which would involve virgin or recidivist offenders and virgin or 

recidivist victims (i.e., the four combinations of potential victimization activity). 

The M,,L entries could be absolute quantitative rates reflecting the respective rates 

of victimization, or they could be more 

general functions reflecting the way those 

rates vary with other exogenous variables. 

These could include contemporary economic conditions, factors in the social 

environment, police deterrent activity like 

preventive patrol, or CJS sanction variables. These functions could be as large and 

as elaborate as could validly be built from 

the available data and statistical evidence. 

(4) CJS resource consumption. As is seen in Figure I, the flow of reported 

crimes and arrestees through the criminal 

justice system is structured similarly to 

JUSSIM I, and the JUSSIM I structure 

could be used for examining the resource 

use associated with this model. The principal extension would involve the incorporation of the victim and offender attributes. 

(5) Rehabilitation (@,r,A,L). The offender 

feedback loop used here is very similar to 

that associated with JUSSIM 11; the 

feedback here, however, is to the victimization event rather than to re-arrest as 

in JUSSIM 11. The feedback is characterized by parameters of recidivism probability or (the complement) desistance probability 

(@,I). These could be introduced as average 

values, or, more richly, as functional forms 

of the exogenous environment in a way 

similar to that discussed previously for victimization events. Effort would be directed 

towards identifying the functional relationships of recidivism probability (I-@,k) 

and the mean time until recidivism (or its 

reciprocal, the mean recidivist crime rate 

(h,~) for the offender subpopulation 

groups. More elaborate functional structures 

could be introduced to account for the 

contemporary socioeconomic environment, 

the criminal justice system's deterrent activity, the nature of the rehabilitation 

treatment offered, and other factors that 

might reflect the individual's prior criminal 

history and his last treatment by the CJS. 

(6) Victim vulnerability (v,~). Just as the 

model displays a feedback process for 

criminal offenders, it also includes a 

feedback loop for victims, with their associated "recidivism" rates. , v,i. ... This rate can be 

affected by factors related to the compensation 

of victims or to restitution by the offender 

or by various types of protective action 

taken after a victimization event in order to 

reduce further victimization. 

(7) Offender-victim-crime-switch process (T).In each cycle through the recidivism process, it is possible for each dimension of the previous path to be transformed. 

First, there is the potential of straightforward transformation of crime type (a 

burglar switches to larceny or a victim of 

robbery has his automobile stolen the next 

time). There can also be transformation of 
both the offender's and the victim's subgroup, either through internal processes, 

such as aging, or by exogenous effects, 

such as change in socioeconomic status 

through change in economic and employment conditions. A large switch matrix, T, 

is included to reflect these transformations. 

(8) Incapacitation effects. Changes in 

incapacitation strategy in the criminal justice system would be reflected through 

branching ratios associated with incarceration (e.g., reflecting the increased use of 

prison) or through the effect of longer sentences on the longer observed time between 

criminal events, with the associated reduction in the individual crime rate (ilk) for 

persons routed through prison. 

(9) General-deterrence eflects. The generaldeterrent effect of sanctions used in 

the criminal justice system (e.g., apprehension probability, conviction probability, probability of imprisonment and sentence) would be reflected through the functional relationships among the sanction 

levels and the virgin criminality (t),the 

desistance probability (@),and the recidivist crime rate (A,k). As these relationships 

develop from the deterrence literature, they 

could be incorporated directly into estimating 

these parameters. 

(10) Environmental factors. It is well 

known that a wide variety of factors in the 

socioeconomic environment are highly 

correlated with crime rates, both crosssectionally and longitudinally. It would be 

extremely desirable to incorporate the 

effect of these factors into the victimization-event functional relationships to reflect the issues surrounding the question of 

the "causes of crime." These factors would 

be reflected in a manner similar to the 

deterrence variables, i.e., through the 

desistance and crime rates associated with 

the recidivist population. If they could be 

adequately identified, these would provide 

important policy bases for crime-control 

actions that go beyond the confines of the 

criminal justice system. As with the other 

relationships in the model, the problems 

relate to the difficulty of estimating these 

relationships, particularly in an identified 

causal form. 

Ill. Structure of the model 

parameters 

The basic variables in the model include the 

following: 

(1) Criminal population, their characteristics, and their criminality. 

(2) Recidivist population and their 

recidivism probabilities and crime rate. 

(3) Victimization population and their 

characteristics. 

(4) Victimization event rates reflected in 

the M matrix. 

(5) Offender-victimcrime switch process. 

(6) Branching ratios of the criminal justice system. 

(7) Resource costs and workloads as 

used in the JUSSIM I model. 

In this sectio?, we examine these various 

groups of variables and the structure associated with estimating these variables from 

available data. In many cases, we try to 

indicate our current best judgment of the 

appropriate data elements in estimating 

these variables, but these will of course 

depend on the degree to which data on the 

indicated variables are available and the 

degree to which they do indeed serve to 

estimate the relevant variables, since they 

could well be augmented by other elements 

or replaced by other more efficient estimating variables. Thus, the specifics of the 

variables identified serve more as illustrations than as the ultimate definitive set that 

will eventually be used. 

A. OSfender population. The offender 

population is characterized by a set of attributes reflecting the demographic and 

socioeconomic characteristics along which 

they are best partitioned to generate subgroups with homogeneous offending rates. 

The presumed relevant attributes include 

the following: 

(1) Demographic variables-age, race, 

sex, marital status. 

(2) Socioeconomic status variableseducation level and income level. 

The demographic variables might include 

binary partitions of race and sex, a threeway split for marital status (never married, 

currently married, and previously married 

but not currently), and some type of grouping for the age variable. For the socioeconomic status variables, an initial estimate 

might include for education (less than 8 

years, 8 to 12 years, 12 years, and more 

than 12 years) and for income (less than 

$5,000 per year, $5,000-$10,000 per year, 

$10,000-$20,000 per year, and more than 

$20,000 per year). In addition, there would 

be a variable reflecting the individual's employability or skill level. 

This potential criminal population would 

give rise to an input of virgin criminals Kk, 

reflecting the number of offenders of the ih 

potential offender group committing crimes 

of type k. 

B. Oflender recidivist population. The 

recidivist population is similarly characterized by a pair of variables, 4,~and h,k, 

where @,k is the probability of desistance of 

a person of type i who last committed a 

crime of type k (where desistance in this 

case implies complete cessation of crime 

committing behavior). In addition, those 

who do continue to commit crimes do so at 

a rate A,k, reflecting the reciprocal of the 

time until the next crime by a person of 

type i who has just previously committed a 

crime of type k. 

The attributes associated with the 

recidivist population could include the 

same ones characterizing the criminal 

population, augmented by the individual's 

prior criminal record (the number of prior 

arrests, convictions, sentences) and by the 

treatment last given him by the criminal 

justice system (failure to arrest, arrest but 

no charge, acquittal at trial, conviction but 

released into community supervision, or 

institutionalization). In any of these, any 

level of detail appropriate to alternative 

specific treatment programs could be 

incorporated into such a model. 

C. Victim population. The structure of the 

victimization population would be developed in a manner similar to that of the 

offender population. The dominant demographic, social, and economic variables 

would include age, race, sex, marital status, 

education level, and income. It may well 

turn out, however, that an examination of 

the detailed data will suggest a different 

structuring of the individual variables for 

the victimization population than for the 

offender population, even though the basic 

variables would be the same. 

In addition, the victimization population would also be characterized by some 

measure of exposure. This measure would 

include a combination of considerations of 

assets or vulnerability to victimization as 

well as considerations of self-protective 

actions taken to reduce the risk of 

victimization. 
D. Rate of victimization events. The rate 

of victimization events is indicated by the 

entries in the victimization matrix, M,,r,the 

rate at which a victim of c1ass.j is victimized 

by an offender of class i for a crime of class 

k. The structure of the matrix isdictated by 

the structure of the offender and victim 

populations. The entries would be the rate 

of aggregate victimizations by aggregate 

offenders (combining the virgins and recidivists of both offender and victim groups). 

The entries in the matrix would be either a 

simple scalar value for the rate of victimization events or, more generally, a function 

of current environmental factors, the deterrent effects of current criminal justice 

sanctions, and the effect of such police 

practices as preventive patrol. 

Examples of the relevant environmental 

factors include: 

(1) Population density as measured by 

people per acre in the district being studied, 

such as a census tract. 

(2) A measure of the housing condition 

in the district, as measured, for example, by 

the persons per room or the measured state 

of dilapidation of the housing in the area. 

(3) A measure of the migratory mobility 

of the population in the area as measured 

by the percent of population resident in the 

area for less than 2 years. 

(4) A measure of the state of unemployment in the area as measured by the percent 

employed, the percent seeking employment 

but unemployed, and the percent eligible 

for employment but no longer seeking 

employment. 

(5) A measure of the state of family 

disintegration in the region as reflected, 

say, in the percent of one-parent families. 

(6) A measure of the differences across 

regions, as measured by a variety of 

regional indicator variables. 

The deterrence variables would be 

reflected through additional functional 

relationships on the M matrix. These 

relationships would include variables such 

as the probability of arrest given a crime, 

the probability of conviction given an 

arrest, the probability of imprisonment 

given conviction, and the mean time served 

for those imprisoned. 

The police crime prevention activities 

might include the intensity of preventive 

patrol (as measured, for example, by the 

mean patrol passage time for a random 

point in the district), by the percentage of 

unmarked patrol activity, as well as by the 

rate of various forms of police crimeprevention activity, such as the use of 

family crisis intervention units. 

To the extent that data do not permit 

determination of the M,]k functions in 

terms of environmental factors and deterrence factors, then these factors should be 

brought into the relationship for determination of the virgin crime-propensity from 

the potential criminal population (0,and 

for the determination of the recidivism 

parameters, A and 4, associated with the 

recidivist offenders. It is probable, however, 

that the relationship will be more easily 

determined for the victimization rates than 

for the offenders, because most criminal 

records do not make an adequate distinction between virgin and recidivist offenders. 

Therefore, the relationship may well be 

more easily applied directly through the 

M,,k matrix than partitioned into separate 

relationships for virgins and recidivists, 

with the recidivists' relationship partitioned 

between the desist probability (4) and the 

associated crime rate, A. 

E. Victim recidivism. Recidivism is built in 

for victims just as it is for offenders. The 

parameters for the victimization recidivism 

process, identified as victimization at a rate 

vJr would be a parameter very similar to A,r 

for the offender recidivists. The victimization-recidivism function would be associated with each victimization population 

group j, and would be designed to incorporate consideration of the victims' prior 

history, just as offenders' prior history is 

taken into account in estimating the recidivism parameters. In addition, v,k would 

take into account the victims' reactions to 

their prior victimization experiences and to 

the compensation or restitution environment. For example, if compensationarrangements tend to reduce the incentives 

for self-protective action, then an environment that provides victim compensation 

would be expected to stimulate a higher 

victimization-recidivism risk. If prior victimization history stimulates self-protective 

action such as target-hardening or escape, 

then the victimization-recidivism rate 

would be reduced correspondingly. 

F. Offender-victim-crime switch. JU SSI M 

I1 calls for a crime-switch matrix reflecting 

the transformation from a prior crime type 

to a subsequent one by recidivists; 

JUSSIM 111 will require a more elaborate 

switch process. First, it must incorporate 

the offender's crime-type switch as in 

JUSSIM 11. It will also require transformations of both the offender class and the 

victim class on subsequent recidivism. 

Thus, an offender would transform from 

type i to i', a victim from type jtoy, and the 

crime type from type k to k'. For example, 

an offender might age, change his education 

level (perhaps because of an educational 

component of his treatment program) 

increase his earnings, or change his marital 

status between successive incidents. The 

switch matrix would therefore reflect those 

rates of state transition. For victims, the 

transition might reflect similar changes in 

demographic structure or changes in 

exposure reflecting various actions taken 

for self protection. The matrix would be a 

square matrix with rank equal to the 

product of the number of offender types by 

the number of victim types by the number 

of crime types on each of its dimensions. 

G. Branching ratios in the criminal justice 

system. For the flow through the criminal 

justice system, JUSSIM 111 requires 

branching ratios similar to those associated 

with JUSSIM I and JUSSIM 11. These 

branching ratios, however, must now 

reflect the much richer "characteristic" or 

"crime-type" structure of the JUSSIM 111 

model. Thus, the branching ratios would 

depend in general on the characteristics of 

the offender, the characteristics of the 

victim, and the crime type. This provides 

the opportunity for reflecting the differential treatment given to offenders or 

defendants based on their different demographic or socioeconomic attributes. It 

also provides the opportunity for reflecting 

the influence of a victim's characteristics on 

the treatment accorded his attackers (e.g., 

reflecting a difference in the courts' 

responses to intergroup events rather than 

to intragroup ones). 

H. Resources, costs, and workloads. The 

JUSSIM 111 model would include data on 

the resource costs and workloads just as 

they are incorporated in the basic JUSSIM 

I format. If the parameters are independent 

of the offender or victim class, their values 

would simply be replicated for that 

segment of the workload vector. If the 

workloads are sensitive to either class, then 

that relationship would be reflected in 

richer detail within the workload vector. 

The resource costs would depend only on 

the resource and would be independent of 

any of the crime type, victim, or offender 

characteristics, as in the previous versions 

of JUSSIM. 
IV. Statistical considerations 

The statistical issues underlying the development of the JUSSIM I11 model pertain 

to the formulation of valid methodological 

strategies for estimating the functional 

relationships which characterize the respective model components. For this 

purpose, attention must be directed to the 

following four basic problems: 

(1) The specification of the structure of 

the data array required for the estimation 

of a particular functional relationship and 

its corresponding parameters. 

(2) The specification of methods of statistical analysis for parameter estimation 

from appropriate data arrays. 

(3) The specification of available data 

sources and their possible limitations as a 

basis for parameter estimation. 

(4) The specification of the potential 

need for new data sources in terms of 

alternative sampling and measurement 

procedures. 

The remainder of this discussion is 

concerned with the implications of these 

considerations for the JUSSIM 111 model. 

A. Spec8cation of data array structure 

for parameter estimation. Since the JUSSIM 

111 model is concerned with the rates of 

occurrence of discrete events (victimizations, arrests, trials, etc.), the data arrays 

required to estimate the various functional 

relationships in its structure are multidimensional contingency tables which link 

the frequencies of such events to the 

characteristics of the corresponding victims, offenders, and environmental subpopulations. In this framework, the 

dependent variables would pertain to the 

outcome (or response) status for exposure 

units at risk for such phenomena as: 

(i) Whether a person of a particular type 

experiences any victimizations during a 

particular time period (the most recent day, 

week, month, year). 

(ii) Whether a person of a particular 

type commits any victimizations during a 

particular time period. 

(iii) Whether a victimization event is 

reported to police by either the involved 

persons or witnesses. 

(iv) Whether a reported victimization 

event ultimately leads to an arrest. 

(v) Whether an arrested person is 

ultimately sent to prison or experiences 

other sanctions. 

(vi) Whether an arrested person commits a subsequent victimization (and/ or is 

re-arrested) or not during a particular time 

period after release from the criminal justice system (either prior to trial, at the end 

of trial, or at the end of prison sentence or 

other sanction). 

(vii) Whether a victimized person experiences a subsequent victimization or not 

during a particular time period after the 

previous victimization. 

The independent variables would reflect 

the specific nature of such exposure units 

as: 

(a) The demographic, socioeconomic, 

and vulnerability characteristics of potential victims. 

(b) The demographic, socioeconomic, 

and opportunity characteristics of potential 

offenders. 

(c) The crime type and the environmental characteristics for reported victimizations together with any available information for the involved victim and offender as 

in (a) and (b). 

(d) The demographic, socioeconomic, 

and ~revious criminal record characteristics-of an arrested person together with 

corresponding information for the involved victim as in (a) and the crime type 

and environment as in (c). 

(e) The demographic, socioeconomic, 

and criminal record characteristics of a 

person released from the criminal justice 

system (either prior to trial, at the end of 

trial, etc.) and their opportunity characteristics for committing subsequent vidmhtions. 

(f) The demographic, socioeconomic, 

previous victimization history, and vulnerability characteristics of a victimized 

person. 

Thus, the parameters in the JUSSIM 111 

model can be estimated through the 

analysis of such contingency tables as: 

(1 (i) vs.(a) to determine the structure 

(3)of the victim population and the 

virgin victimization rates {q,k). 

(2) (ii) vs. (b) to determine the structure 

{s,L)of the offender population and virgin 

offender rates {hk). 

(3) (iii) vs. (a) and (iii) vs. (b) to 

determine the reporting rate structure for 

victimizations from the victim and offender perspectives. 

(4) (iv) vs. (c) to determine the arrest 

rate structure for reported victimizations. 

(5) (v) vs. (d) to determine the prison 

rate structure for arrests. 

(6) (vi) vs. (e) to determine the recidivism rate structure {h,k)and the desist rate 

structure {4,k). 

(7) (vii) vs. (0to determine the victimization recurrence rate structure { vjk). 

Similarly, if simultaneous information for 

both the offender and victim can be 

obtained for individual victimization events 

and consecutive pairs of victimization 

events, appropriate contingency tables can 

also be formulated to determine the 

victimization rate structure ~{,]k) and the 

crime switch structure {T,k,,tllk;,~~ll~k

respectively. More realistically, hqwever, 

such data would be very difficult, if not 

impossible, to obtain. For this reason, a 

more practical estimation strategy may be 

to apply synthetic estimation ("raking") 

procedures (as described in Appendix A) to 

adjust analogous arrest data like (d) to the 

corresponding separate marginal structures for victims and offenders like the 

{vk)and {S,k). However, as indicated in 

the next section, such methods should be 

used cautiously because they presume that 

the joint victim-offender crime association 

structure for victimizations is the same as 

for arrests. 

In summary, various types of multidimensional contingency tables can be constructed as a basis for estimating the 

parameters in the JUSSIM 111 model. 

Some of these tables may involve rather 

crude data while others may require highly 

sophisticated data. In either situation, the 

critical issue is the formulation of such 

estimation problems in terms of contingency tables which can then be manipulated via the methods of analysis in 

Appendix A to determine the functional 

relationships which characterize the model 

components. In any event, a considerable 

effort in data collection, analysis and 

assumption testing can be anticipated 

before valid and credible relationships are 

developed. 

B. Specification of available data sources. 

The JUSSIM 111 model described in this 

paper is extremely elaborate in order to 

account for the diversity of victim types, 

offender types, and crime types. For this 

reason, obtaining data for the formal construction of the model will require 

extensive use of available data sources as 

well as the development of new data 

sources in the future. In this section, 

various existing data sources are discussed 

in terms of their applicability to the 

JUSSIM 111 model. 

The FBI's Unljbrm Crime Reports (UCR) 

present basic data for police reported 

crime rates in different parts of the United 

States. The corresponding arrest data 

provide some inforniation concerning offender demographic status as well as the 

environmental situations in which the re- 
spective crimes have occurred. On the 

other hand, the principal limitation of 

these data is that the arrest process can 

involve a biased selection of the offender 

population, some offenders being more 

arresi prone than others. Thus, estimates 

obtained from the UCR data for offender 

characteristics need to be contrasted with 

corresponding results from other sources 

of information like victimization surveys 

and offender self-report studies in order to 

evaluate the general magnitude of this bias. 

Such comparisons also provide a basis for 

the adjustment of competing estimators 

from alternative data sources to a common 

framework by synthetic estimation (raking) procedures as described in Appendix 

A. Other comparisons of UCR crime data 

with victimization data and offender selfreport data can be used to estimate the extent to which various crime types are 

reported or not reported to the police. 

The victimization surveys provide the primary sources of information for estimating 

functional relationships in the victimization process. In addition, victim recidivism information is potentially obtainable 

from the longitudinal aspects of the national survey, which obtains information 

repeatedly from panel members. The panel 

data could be used to construct estimates 

for the intervals between victimizations or 

the rate of victimization and the nature of 

the crime switch process for victims. All of 

this analysis, however, should be undertaken with caution because of the errors 

with which individuals recall victimization 

events, especially sequences of such events. 

Where available, the Offender Based 

Transaction Statistics (OBTS) are particularly well suited as data sources for the 

branching ratios throughout the criminal 

justice system. Typically, these can be estimated for each of the offender demographic groups since the OBTS incorporate offender characteristics as part of the 

regular record. If the OBTS contain some 

limited victimization information, such 

data might provide preliminary estimates 

for the interactions in the joint offendervictim victimization rate structure. 

Another relevant information source is the 

criminal history record or "rap sheet." 

These records typically include data on the 

age, race, sex, and possibly other demographic characteristics of the offenders, as 

well as the sequence of offenses for which 

they were arrested, the dates of arrest, and, 

when reported, the disposition of each 

arrest. Thus they provide a basis for the 

estimation of the recidivism behavior of 

offenders. The rap sheet data and the 

OBTS data are largely complementary. 

They also provide some opportunities for 

consistency checks, but they are not likely 

to be available for all offenders in all jurisdictions for a long time to come. Special 

adjustment procedures will be required to 

use such data in jurisdictions other than the 

few for which good data are available. 

Other aspects of criminal history, like nonreported offenses or offenses for which no 

arrests were made, can be analyzed with 

offender self-reports. Such self-reports are 

unquestionably suspect a priori, but further study is required to determine the 

degree to which there is distortion in the 

self-reporting process (both suppression 

and elaboration) and to identify methods 

for adjusting for such distortions. In this 

context, the most important use of selfreport information would be the estimation of association parameters for offender 

characteristics which could then be synthesized with analogous data from rap sheets 

and from victimization surveys. 

In summary, these available data sources 

provide a basis for estimating in at least a 

preliminary way many of the parameters of 

the JUSSIM 111 model, even in the face of 

their respective limitations and even 

though none of them is available at the victim-offender-crime level of detail for 

victimization events. Moreover, a wide variety of special-purpose studies (e.g., the 

Kansas City Police Patrol Experiment 

1974, the Wolfgang, Figlio, and Sellin 1972 

birth cohort study, etc.) represent additional sources of information for estima- 

.ting various parameters after appropriate 

adjustments have been made for their 

special character or the particular jurisdiction where they took place. Thus, although 

suitable caution must be exercised, existing 

data sources can be used to form preliminary estimates for various functional 

relationships in the JUSSIM 111 model, 

and those estimates will stimulate the collection of better data and the improved 

specification of relationships, eventually 

resulting in a reasonable and useful 

formulation. 

C. Specification of new data sources. A 

primary motivation underlying the formulation of the JUSSIM 111 model is its 

potential usefulness as a planning instrument for criminal justice system policy 

decisions. However, this type of application is appropriate only if the estimated 

functional relationships in the model are 

based on valid data. Thus, the inherent 

weaknesses of the existing sources of information, like those described previously in 

Section IV. B, imply the need for new data 

collection systems havingless selection bias 

in their sampling procedures and more 

accurate measurements. From a statistical 

point of view, each of the respective types 

of contingency tables (1)-(7) described in 

Section IV.B, together with the corresponding dependent variables (i)-(vii) and 

independent variables (a)-(f), should be 

considered in this light, edch requiring 

detailed specifications to obtain data with 

the required validity. Thus, a realistic discussion of the development of the new 

information sources required warrants a 

separate research effort beyond the scope 

of this paper. Nevertheless, some brief remarks about the general requirements for 

such data collection efforts can be given to 

motivate those future investigations. 

First of all, attention should be directed 

toward improving the quality of the data 

pertaining to the processing of arrests 

through the criminal justice system. A 

national sample of jurisdictions will be 

needed in order to obtain complete followup information on the ultimate disposition 

(e.g., dismissal before trial, acquittal after 

trial, probation after conviction, prison 

sentence of specific duration) for an appropriately defined parallel set of stratified 

subsamples of different types of arrests 

(e.g., all homicides, 30% of all other felonies, 10% of all misdemeanors, etc.). 

Moreover, such data should be collected in 

a manner which is not biased by the 

selected police departments and courts, 

does not interfere with their everyday 

operation, and encourages their cooperation and participation. 
1 I
 Table 1. Predicted values for prison rates from linear model contingency table analysis 

I- Defendants Predicted Prior Arrest Total offense1 arrests promptness2 lncome3 Defendants Steon',":?,"," prison 


rate 


NRB One or more S L 

NRB One or more S HU 

NRB One or more A L 

NRB One or more A H U 

NRB None S L 

NRB None S H U 

NRB None A L 

NRB None A H U 

RB One or more S L 

RB One or more S H U 

RB One or more A L 

RE One or more A H U 

RB None 

RB None 

R B None 

R B None 

OFML One or more 

OFML One or more 

OFML One or more 

OFML One or more 

OFML None 

OFML None 

OFML None 

OFML None 

NRB = nonres, burg.; RE = res. burg.; Residual goodness of fit O (D.F.=21) = 6.01 

OFML = larceny (felony and misdemeanor) Total variation 12(D.F.=23) = 87.71 

2~ = arrest same day as offense; A = later day 

3~ = low; HU = high or unclassified 

Secondly, a national sample similar to that 

described for arrests will be needed for 

information on the subsequent experience 

of convicted offenders who are released 

from the criminal justice system via probation, parole, or other means. This information source would also involve a multistage selection beginning with institutions, 

such as courts, full probation, halfway 

houses, and prisons, and ultimately 

focusing on released offenders. Various 

types of data would then be collected for 

the individuals in the sample by both active 

(interview) and passive (reports of subsequent arrests by the police or FBI) methods 

for a particular fixed future time period of 

perhaps as long as 10 years. 

The formulation of new information 

sources about the arrest process, although 

perhaps prohibitively expensive in practice, is straightforward in principle. The 

questions pertaining to improving the 

quality of victimization data are considerably more difficult. Thecritical issue here is 

that victimizations are publicly perceived 

at an aggregate level (for instance, a 1-

month time period for all persons who live 

in a specific census tract) as relatively 

prevalent events, but are experienced as 

very rare events by specific individuals for 

such isolated time periods as 1 week or 1 

month. Thus, data collection systems like 

the victimization surveys which focus on 

the recent experience of selected individuals can provide only a limited amount of 

information about the reported victimizations themselves (ignoring temporarily the 

corresponding measurement error problems) because of the relatively small 

number who are involved even in verv . large - samples. They do, however, provide useful 

information about different types of 

victimization rates in the exposed population at risk. Thus, another data source is 

needed for obtaining more extensive 

coverage of victimization events. One system which could be developed for this purpose would be a national system of victimization reporting centers whose locations 

were based on an appropriate sampling 

plan. The explicit mission of these centers 

would be to provide free counseling and 

legal advice in a confidential manner (i.e., 

without specific notification to the police 

or other official agencies) to both offenders 

and victims; and their implicit mission 

would be to obtain information about the 

Percent unexplained variation = 7% 

corresponding victimization events and 

possibly previous events. Obviously, the 

principal disadvantage of this data source 

would be the bias associated with its reliance on volunteer reporting. Nevertheless, 

if the reporting rates for victimizations 

were high, then the effects of this bias might 

be reduced by using matching procedures 

to link such information to that obtained 

from police records and victimization 

surveys and applying multiple-recordsystem statistical estimation procedures 

like those described in Bishop, Fienberg, 

and Holland (1975, Chapter 6), Koch, ElKhorazaty, and Lewis (1976a), and Marks, 

Seltzer. and Krotki (1974). 

Finally, other types of new information 

systems may be of interest with respect to 

certain specific aspects of victimization 

events. In this regard, a national sample of 

long-term cohort studies on virgin victimizations would provide useful data similar 

to that provided by Wolfgang, Figlio, and 
Sellin (1972) on virgin offenses. Moreover, 

a national follow-up sample for suitably 

identified victims who are linked to arrests 

or other methods of reporting might 

obtain information about their subsequent 

victimization experience. 

In summary, the formulation of aJUSSIM 

111 model helps to identify several new 

sources of data for the measurement of 

crime and the activities of the criminal justice system. A broad range of possibilities 

exists for the design of such future 

information systems, but their specific 

development requires a substantially more 

comprehensive investigation. The JUSSIM 

I11 model sketched here represents an important instrument for generating an 

agenda of future research in the develop 

ment of criminal justice statistics for use in 

the planning process. 

Appendix A: 

Specification of methods 

of statistical analysis 

The principal objective underlying statistical 

analyses for contingency tables such as (1)-(7) in 

Section 1V.A pertains to the characterization of 

the relationship between dependent outcome 

variables such as (i)-(vii) and correspondingsets 

of independent variables such as (a)-(f). Attention is directed at identifying which of the 

independent variables account for the variation 

in the respective dependent variables together 

with the extent of the interaction among them. 

One approach for dealing with these questions is 

given in Clarke and Koch (1975), who considered the relationship between the probability of 

prison sentence and independent variables corresponding to the defendent's age, race, sex, 

income, employment, type of offense charged, 

prior arrest record, and arrest promptness (a 

proxy for strength of evidence against the 

defendant) for a sample of certain types of 

burglary and larceny arrests occurring in 

Mecklenburg County (Charlotte), North Carolina, 

during 1971. Their analysis consisted of two 

phases: 

Phase I: A screening of the variables to select 

those responsible for the greatest amount of 

variation in prison rates among the subpopulations defined by different combinations of the 

independent variables. 

Phase II: The fitting of a parsimonious model 

involving the independent variables selected as 

important during Phase 1. 

Phase I was conducted in the same spirit as stepwise multiple regression, but in a context appropriate for the categorical nature of the discrete 

variables under investigation. In this regard, certain Pearson Xz-statistics divided by their 

respective degrees of freedom were used like the 

"F to enter" statistic in multiple regression as 

measures of relative importance for suitably 

eligible combinations of variables in a multivariate relationship. The first variable selected 

was the one having the largest (x2/d.f.) with 

respect to its first-order (two-way) relationship 

to prison outcome. Additional variables were 

selected by applying a similar selection rule using 

(x2/d.f.) computed for three-way, four-way, etc. 

contingency tables involving all of the 

previously selected independent variables successively with each of the eligible remainingvariables vs. prison outcome. Phase 1 alsoincluded a 

procedure for terminating the selection process 

when the remaining variables were not statistically important. Two different types of statistics were used for this purpose: 

(A) The Pearson X2-statistics for the partial 

association (from two-way contingency tables) 

of a specific eligible variable vs. prison outcome 

summed over all possible combinations of variables that have already been selected. 

(B) A Xz-statistic developed by Cochran 

(1954) and Mantel and Haenszel (1959), which 

combines information with respect to the effect 

of a specific eligible variable on prison outcome 

over all combinations of previously selected 

wriables. 

The statistic (A) reflects both the main effects of 

a specific variable and its interactions with previously selected variables. After the first few steps 

of the selection process, this statistic tends tolose 

its usefulness for two reasons. First, its degrees 

of freedom increase rapidly causing selection to 

become overly stringent. Second, the data become thinned to the extent that many of the cell 

frequencies in the multidimensional contingency 

table become smaller than 5 so that this criterion 

begins to lose its validity as a chi-squarestatistic. 

At this point, statistic (B) becomes useful 

because it combines information across all 

combinations of previously selected variables 

and is thus more resistant to the thinning 

problem. This statistic is highly sensitive with 

respect to detecting weak but consistent 

relationships for variables which have not yet 

been selected; however, it has the disadvantage 

that it reflects the "average"effects of a variable 

as opposed to its "total contribution," which 

includes interactions with other variables. For 

the most part, this difficulty should not often 

pose a major problem because statistic (A), 

which is used in the earlier stages, does pertain to 

the "total contribution" of a variable. In the later 

stages of the selection process where statistic (B) 

is used, the "average effects" of variables are the 

ones of primary interest becausethe interactions 

with other variables are likely to be of minor 

importance because the relationships to which 

they apply are generally weaker. In summary, 

statistic (A) is used to decide whether to terminate selection after the first two or three variables have been selected, and statistic (B) is used 

thereafter. In each case, the basis for terminating 

selection is failure to meet a significance level of 

a = 0.10 or a = 0.05, as in forward stepwise regression. Finally, in some situations, certain 

variables are known apriori to be of importance. 

These can be included either at the beginning of 

Phase 1 or at the end, depending on their potential causal role with regard to the dependent 

variable. 

For the burglary and larceny arrest data considered by Clarke and Koch (1975), Phase I led to 

the selection of type of offense, income, prior 

arrest record, and arrest promptness, respectively. These four variables were then crosstabulated with prison status to produce a fivedimensional contingency table. Phase I1 then 

involved the fitting of a model to the prison rates 

for all combinations of the selected independent 

variables. For this purpose, the weighted least 

squares methods described in Grizzle, Starmer, 

and Koch (1969) were used to formulate an effective additive linear model for characterizing 

the variation among prison rates by systematically removing unimportant sources of variation 

such as higher order interaction effects. Such 

effects are not retained unless they are significant 

at an appropriate level like a = 0.05. In addition, 

the model is not considered to be satisfactory 

until a residual goodness of fit statistic Q 

becpmes small (i.e., not significant at a = 0.25), 

for otherwise not all of the important sources of 

variation have been identified. A final criterion 

for model effectiveness is a measure of unexplained variation, analogous to (I - R~)in multiple regression, which is defined as the ratio of 

the goodness of fit statistic for the model to an 

analogous statistic for total variation among all 

the prison rates (i.e., the goodness of fit statistic 

for a model which implied that all the rates were 

equal). U 

Analyzing prison rate data in this way leads toan 

efficient description or smoothing of the data as shown in Table 1. These results indicate that the 

functional relationship between prison status 

and the independent variables which were 

included in the analysis can be summarized in 

terms of four distinct predicted values or clusters 

as follows: 

Cluster I. High prison rate = 53.7 percent if 

nonresidential burglary and low income and 

arrested same day as offense. 

CIusrer 2. Moderate prison rate = 30.4 

percent if nonresidential burglary and (a) low 

income but not arrested same day, or (b) arrested 

same day but not low income, or (c) one or more 

arrests but not low income and not arrested same 

day, etc. 

Cluster 3. Low prison rate = 19.3 percent ry 

larceny and one or more arrests and low income. 

Cluster 4. Very low prison rate= 7.2 percent if 

not in Clusters 1, 2, or 3. 

These "predicted values" are different only if 

the corresponding observed values are significantly different; moreover, they represent better 

estimates (i.e., with smaller standard errors) of 

the prison outcome probabilities than the actual 

observed rates for the respective subpopulations 

corresponding to the cross-classified independent variables, because they are based on the 

entire set of data rather than on its component 

subsets. Thus, a clearer and more simplified 

framework is obtained for interpreting the rela- 
tive effects of the important independent 

variables than would be possible from casual 

inspection of the full multidimensional contingency table. 

An alternative framework for Phase 11 analysis 

is based on the use of log-linear models. These 

types of funct~onal relationships are discussed 

extensively in Bishop, Fienberg, and Holland 

(1975), Goodman (1970, 1971), and Ku and 

Kullback (1974). They can often be applied to 

contingency tables such as the previously considered prisondata by the Deming-StephanIterative Proportional Fitting procedure in conjunction with an appropriate set of marginal 

subtables. For this reason, the resulting estimated parameters have reasonably robust and 

stable statistical properties even for sparse contingency tables (w~th many small frequencies 

which are less than 5). Their major disadvantage 

is the possibly unclear interpretation of the loglinear model parameters, particularly when 

interaction is present in the relationships among 

the dependent and independent variables. 

Further discussion of the relative merits of linear 

vs. log-linear models is given in Bhapkar and 

Koch (1968a, 1968b). This subject is alsoconsidered in Koch et al. (1976b) In the context of a 

general methodolog~cal strategy for estimating 

log-linear model parameters, which is based on 

the simultaneous use of weighted least squares 

and lterative Proport~onal Fitting or other 

related computational algorithms. 

Another statistical method of potential use with 

respect to the JUSSIM 111 model is synthetic 

estimation ( or "raking") for contingency tables. 

This analytical procedure permits an observed 

table corresponding to a sample from a specific 

population to be adjusted to yield estimators for 

other target populations, e.g., (I) local or regional subdivisions of a sampled national population; 

(2) other local or national populations which 

partially overlap a sampled local population. 

The assumptions required for the validity of this 

approach are: 

(I) Certain. marginal distributions for the target population, referred to as the "allocation 

structure," are known on the basis of census or 

other data. 

(2) The higher order interactions across the 

subsets in (I), referred to as the "association 

structure,"are the same for the target population 

as for the sampled population. 

Given these considerations, the estimated 

table for the-target population can be obtained 

by using the Deming-Stephan Iterative Proportional Fitting algorithm which preserves 'association structure" as it successively adjusts the 

observed table to the components of the "allocation structure." Additional details pertaining 

to the statistical properties of this procedure are 

given in Bishop, Fienberg, and Holland (1975). 

Causey (1972), Ireland and Kullback (1968),and 

Freeman and Koch (1976). As indicated by 

Seidman (1975) in a more general context, such 

synthetic estimation methods should be used 

cautiously because of the potentially severe bias 

they may suffer when assumptions (I) or(2) are 

not justified or are incorrectly applied. 

Finally, Kochetal. (1975)and Brock etal. (1975) 

discuss weighted least squares methods of 

analysis for contingency tables based on complex sample surveys such as those used to 

measure victimization. These procedures are 

directly analogous to those described in reference to the prison rate from Clarke and Koch 

(1975). 

In summary, a broad range of statistical methods are available to estimate functional relationships for the components of the JUSSIM I11 

model. Some of these are based on weighted 

least squares computations while others are 

based on the Deming-Stephan Iterative Proportional Fitting procedure. Thus, for any specific 

application, the critical issue is to use that method which is most appropriate to the estimation 

problem under consideration. 

References 

Belkin, Jacob, A. Blumstein, and W. Glass 

(1971) 

"JUSSIM, an interactive computer program 

for analysis of criminal justice systems." Urban 

Systems Institute Report, School of Urban and 

Public Affairs, Carnegie-Mellon University, 

July 1971. 

Belkin, Jacob, A. Blumstein, and W. Glass 

(1974) 

"JUSSIM 11, an interactive feedback model 

for criminal justice planning. Urban Systems 

Institute Report, School of Urban and Public 

Affairs, Cainegie- ello on University, January 

1974. 

Bhapkar, V. P. and G. G. Koch (1968a) 

"Hypotheses of 'no interaction' in multidimensional contingency tables." Technometrics 

10:107-123. 

Bhapkar, V. P., and G. G. Koch (1968b) 

"On the hypotheses of 'no interaction'in contingency tables." Biometrics 24:567-594. 

Bishop, Y. M. M., S. E. Fienberg, and P. W. 

Holland (1975) 

Discrete multivariate ana!vsis: Theory and 

practice. Cambridge, Mass.: M.I.T. Press. 

Blumstein, Alfred (1975) 

"A model to aid in planningfor the total criminal justice system." In Quantitative tools for 

crimrnal justice planning, Washington, D.C.: 

U.S. Department of Justice, Law Enforcement 

Assistance Administration. 

Brock, D. B., D. H. Freeman, Jr., J. L. Freeman, 

and G. G. Koch (1975) 

"An application of categorical data analysis to 

the National Health Interview Survey." Proceedings of the Social Statistics Section of the 

American Statistical Association. 

Causey, B. C. (1972) 


"Sensitivity of raked contingency table totals to 


changes in problem conditions." The Annals of 


Mathematical Statistics 43:656-658. 


Clarke, S. H., and G. G. Koch (1975) 


"Who goes to prison? The likelihood of receiving 


an active sentence." Popular Government 


41:25-37. 


Cohen, Jacqueline, et al. (1973) 

"Implementation of the JUSSIM model in a 

criminal justice planning agency." Journal of 

Research in Crime and Delinquency, June 1973. 

Cochran, W. G. (1954) 

"Some methods of strengthening the common 

X' test." Biornetrics 10:417-451. 

Freeman, D. H., Jr., and G. G. Koch (1976) 

"The asymptotic covariance structure of estimated parameters from marginal adjustment 

(raking) of contingency tables." 1976 Proceedings of the Social Statistics Section of the 

American Statistical Association 330-335. 

Goodman, L. A. (1970) 

"The multivariate analysis of qualitative data: 

Interactions among multiple classifications." 

Journal of the American Statistical Association 

65:226-256. 

Goodman, L. A. (1971) 

"The analysis of multidimensional contingency tables; stepwise procedures and direct 

estimation methods for building - models for

multiple classifications." Technometrics 13: 

33-6 1. 

Grizzle, J. E., C. F. Starmer, and G. G. Koch 

( 1969) 

"Analysis of categorical data by linear 

models." Biornetrics 25:489-504. 

Ireland, C. T., and S. Kullback (1968) 

"Minimum discrimination information estimation." Biornetrics 24:707-7 13. 

Kelling, G. L., T. Pate, D. Dieckman, and C. E. 

Brown (1974) 

The Kansas City Preventive Patrol Experiment: A technical report. Washington, D.C.: 

Police Foundation. 

Koch, G. G., D. H. Freeman, Jr., and J. L. 

Freeman (1975) 

"Strategies in the multivariate analysis of data 

from complex surveys." InternationalStatistical 

Review 43:59-78. 

Koch, G. G., M. N. El-Khorazaty, and A. L. 

Lewis (1976a) 

"The asymptotic covariance structure of loglinear model estimated parameters for the 

multiple recapture census." Communications in 

Statistics A-5: 1425-1445. 

Koch, G. G., D. H. Freeman, Jr., P. B. Imrey, 

and H. D. Tolley (1976b) 

"The asymptotic covariance structure of estimated parameters from contingency table loglinear models." Proceeding of 9th International 

Biometric Conference, Cambridge, Mass., August 

1976. 

Ku, H. H., and S. Kullback (1974) 

"Log-linear models in contingency table analysis." The American Statistician 28: 1 15-1 22. 

Mantel, N., and W. Haenszel (1959) 

"Statistical aspects of the analysis of data 

from retrospective studies of disease." Journalof 

the National Cancer Institute 22:719-748. 

Mark, E. S.. W. Seltzer,and K. J. Krotki (1974) 

Population growth estimation. New York: 

The Population Council. 

Seidman, D. (1975) 

"Simulation of public opinion: A caveat." 

Public Opinion Quarterlv 39:33 1-342. 

Uniform Crime Reports (1 973) 

Washington, D.C.: Federal Bureau of Investigation, U.S. Department of Justice. 

Wolfgang, M. E., R. M. Figlio, and T. Sellin 

(1972) 

Delinquenc:~ in a birth cohort. Chicago and 

London: University of Chicago Press. 
Redesigning the Kansas City 

Preventive Patrol Experiment 

STEPHENE. FIENBERG 

Department of Statistics 

and Department of Social Science 

Carnegie- Mellon University 

KINLEYLARNTZ 

Department of Applied Statistics 

University of Minnesota 

ALBERTJ. REISS,JR. 

Department of Sociology 

Yale University 

The most striking result of the Kansas City 

Preventive Patrol Experiment (KCPPE) 

was that no significant differences were 

found among the three types of beats ("reactive," "control," and "proactive") in 

reported crime, rates of victimization, level 

of citizen fear, or level of citizen 

satisfaction with the police. In this paper, 

we focus on several related shortcomings of 

the design and implementation of the 

KCPPE. These include (1) the orientation 

toward proving rather than disproving the 

null hypothesis of no differences among 

treatment effects, (2) the confusion of manpower differences and treatment (patrol 

strategy) differences, and (3) the lack of 

control of other variables affecting the 

outcome of the experiment and the lack of 

proper randomization in assigning treatments to beats. Following this discussion 

of the KCPPE, we outline the design of a 

class of randomized controlled field studies 

for patrol-related experiments that are 

adaptable to most large citiesand thatcould 

have yielded considerably more information than the actual design used in Kansas 

City. 

I. The Kansas City experiment 

From October 1, 1972, through September 

30, 1973, the Kansas City, Missouri, Police 

Department conducted an experiment 

designed to assess the impact of routine 

preventive patrol on the incidence of crime 

and the public's fear of crime. The experiment involved 3 variations in the level of 

preventive patrol used in 15 of the 25 beats 

comprising the Kansas City South Patrol 

Division. The 15beats were blocked into 5 

groups of 3 matched beats each, on the 

basis of reported crime counts, calls for 

police service, and demographic data. 

Within each triplet one beat, the "control," 

was to be patrolled by a single police car in 

the usual fashion whenever it was not 

answering calls. In a second beat in each 

triplet, routine preventive patrol was 

eliminated and officers were to respond 

only to calls for service. These were 

referred to as the "reactive" beats. Finally, 

in the third beat in each triplet, routinepreventive patrol was increased to 2 or 3 times 

the usual level. These were referred to as 

the "proactive" beats. Complete details of 

the experimental design and its implementation can be found in Kelling et al. 

(1974). 

The strik.ing result of this Kansas City Preventive Patrol Experiment (KCPPE) was 

that there were no "significant" differences 

among the three types of beats in reported 

crime, rates of victimization, level of citizen 

fear, and level of citizen satisfaction with 

the police. There was simply no apparent 

effect that could be related todifferences in 

patrol manpower allocation, deployment, 

and operation. Now this result appears to 

fly in the face of conventional wisdom that 

increases in police patrol should reduce the 

levels of street crimes such as robbery and 

automobile theft. Since one of the purposes 

of the experiment was "to determine 

whether the Kansas City Police Department 

could safely divert resources ordinarily 

allocated to routine preventive patrol to 

other, possibly more productive patrol 

strategies," the results would appear to 

have important policy implications regarding 

the use of various manpower allocation 

schemes. It is therefore incumbent upon us 

to reexamine the experimental setup and 

the results of the KCPPE with great care in 

order to determine: 

(a) what explanatory model lay behind 

the KCPPE. 

(b) what was measured and what was not 

measured. 

(c) what the results really were. 

(d) what aspects of the experimental 

design and its execution may have led 

directly to these results. 

(e) whether the foregoing facts may in 

any way compromise the conclusions 

reached by Kelling and his coworkers and 

others commenting on the experiment. 

(f) if the conclusions are compromised, 

whether there is a different experiment that 

an appropriate police department might 

conduct which would get around many of 

the problems associated with the KCPPE. 

A major difficulty with the KCPPE and 

any consideration of it are the terms "prevention" and "preventive patrol." Basically, the problem is that "prevention" is a 

black box, and exactly what police officers 

do with time spent on what is called "preventive patrol" is difficult to determine. 

The KCPPE did not actually manipulate 

this elusive concept of preventive patrol. 

Rather, the experiment attempted to manipulate the amount of manpower and its 

deployment. We return to this issue in the 

foilowing sections. 

II. Experimenting 

with police manpower 

Most social experiments, especially those 

involving the police, are not really experiments in the statistical sense, but are in fact 

innovations for which there are no direct 

means available for separating out or con- 
trolling the effects of a change in public 

policy from concomitant changes in related 

variables. For example, "Operation 25," a 

4-month "experiment" conducted by the 

New York City Police Department in 1954, 

involved the more than doubling of police 

strength in Manhattan's 25th Precinct. 

Although reported street crime went down 

markedly over this 4-month period, no 

direct information was available for the 

true crime rates. Alternate explanations of 

the observed decrease were available, and 

no effort was made to assess the possible 

deleterious effects of the increased manpower on adjacent areas or to determine 

what the reported crime would have been 

had the changes in manpower not been instituted. Far better than "Operation 25" 

was the 1966 experiment in New York's 

20th Precinct (see Press 1971, 1972), although it too had its problems. Other 

examples of innovations in police practice 

are readily available. In 1953, the Kansas 

City Police Department carried out a complete 24-hour changeover from two-man to 

one-man patrol cars, and the 24 patrol 

areas were reorganized into 41 substantially smaller beats (see Brannon 1956). No 

adequate evaluation of such a change was 

possible. 

In light (or perhaps we should say shadow) 

of these earlier attempts to evaluate the 

effects of changes in police patrol practices, 

the KCPPE would appear to provide a 

model worthy of careful study. Patrick 

Murphy, President of the Police Foundation which supported the KCPPE, has 

been quoted as saying that the preventive 

patrol project "ranks among the very few 

major social experiments ever to be completed and was unique in that never before 

had there been an attempt to determine 

through such extensive scientific evaluation the value of visible police patrol." 

While the KCPPE does not quite measure 

up to the well-evaluated randomized controlled field trials of large-scale social 

action programs described by Gilbert, 

Light, and Mosteller (1975), it represents a 

major step forward in the design and strategy of police research. It is only because of 

the use of sophisticated statistical techniques and their extensive documentation 

in the Technical Report (Kelling et al. 

1974) that we are able to assess very carefully the various aspects of design and 

analysis. The KCPPE has not only shown 

that a police department can successfully 

experiment with patrol strategies without 

disastrous consequences, but it has also 

provided a starting point for future experimentation in this area. 

Ill. Shortcomings of the KCPPE 

Our discussion of the design and analysis of 

the KCPPE here focuses on several 

interrelated issues: 

(1) proving rather than disproving the 

null hypothesis. 

(2) the difficulty in actually assessing the 

treatment differentiation. 

(3) the absence of adequate measurement of treatment implementation. 

(4) the confusing of manpower differences and treatment (patrol strategy) 

differences. 

(5) the possible contamination of data 

in experimental beats by the patrolling 

strategies in adjacent beats (whether they 

be experimental or not). 

(6) the lack of proper randomization in 

assigning treatments to beats. 

A. Proving the null hypothesis 

A primary purpose of carefully designed 

statistical experiments is to control for as 

many sources of variation as possible in 

order to maximize the probability of 

detecting differences in the effects of 

different treatments when these differences 

do in fact exist. Because the KCPPE was 

unable to detect*any differences in outcome 

attributable to the differences in the level of 

preventive patrol, we must therefore ask 

whether this result is due to the true lack of 

treatment effect differences or simply the 

weakness of the experimental setup when 

in fact differences do exist. The framework 

of hypothesis testing adopted by the authors in their report is geared toward 

rejecting the null hypothesis (in this case 

that of no difference) in favor of some 

alternative, by giving heavy weight to the 

null hypothesis unless it is demonstrably 

false. In technical terms we fix the level of 

significance (the probability of falsely rejecting the null hypothesis) at some low 

value (e.g., a = 0.05) and the probability of 

failing to detect the alternative hypothesis 

when it is true is determined. Unless the 

latter is also small, we end up weighting the 

experiment in favor of the null hypothesis. 

The danger of "proving" the null hypothesis by means of a weak experiment haunts 

much of the literature on social experimentation. 

Because the no-difference outcome of the 

KCPPE has such important social and policy implications, it is important to ask 

whether the design chosen sufficiently controls for crucial sources of variability to 

allow for the detection of the effects of true 

treatment differences when they exist. 

The following example, adapted* from 

Kempthorne (1952), may help clarify the 

issues just raised. A soft drink manufacturer has developed a new procedure for 

producing its best-selling cola. The question to be resolved is whether or not people 

can detect a difference in taste between the 

colas produced by the new and old procedures. The manufacturer's statistician sets 

up the following experiment. A panel of n = 6 tasters is presented with 3 glasses of cola, 

2 produced by the old process and 1 by the 

new. Each taster is asked to pick the one 

cola whose taste differs from the other two. 

The tasters work independently of one another, and the colas are presented in a random order to each taster. The null hypothesis, Ho,specified by the statistician is that 

"no differences are detectable," and when 

MI is true the probability of detecting the 

cola produced by the new process isp = 113. 

There are 7 possible results of this experiment, indexed by the number of tasters 

who correctly picked the cola from the new 

process. llnder fi, the probabilities of 

observing these results are: 

No. correct Probability 

6 11729 = 0.001 

5 121729 = 0.016 

4 601729 = 0.082 

3 1601729 = 0.219 

2 2401729 = 0.329 

If all 6 tasters correctly pick the cola from 

the new process then we would appear to 

have strong evidence that HOis false. Even 

if only 5 tasters are correct the evidence is 

strong, but if only 4 tasters are correct, we 

might have observed a result so extreme 

with probability 0.001 + 0.016 + 0.082 = 

0.099 0.1. This is not a very rare event 

and, even if a small difference between the 

colas exists, we would likely not take the 

result of 4 out of 6 as being indicative of 

such a difference. Thus we take 5 or 6 correct as evidence against Ho and in favor of 

some alternative hypothesis. 

In order to evaluate how good an experiment this really is, we need to ask what 

would happen if some alternative to HCis 

really true. Suppose, for example that p = 
112, and the cola from the new process is 

more likely to be picked than is indicated 

by fi.Then the probability of getting5 or 6 

correct is now (1 / 64) +(6164) ~0.109. Thus 

even though there is a difference we would 

fail to detect it about 8 out of 9 times using 

our criterion of 5 or 6 correct. The 

probability 0.109 is referred toas thepower 

of our test for the alternativep = 112, and in 

the present case it would appear that the 

experiment as planned will simply not be 

powerful enough to detect an alternative as 

big asp = 213 (for which the power is only 

0.35). The experiment appears to be 

stacked in favor of the null hypothesis, and 

unless we are careful we might erroneously 

conclude that p = 113 even when it really is 

as large as p = 213. Note the importance 

here of explicitly stating what effects we 

would like to be able to detect if they are 

present. 

Basically, there are three ways to make an 

experiment more sensitive to detecting 

reasonable alternatives to H,: 

(1) increase the sample size. 

(2) reorganize the structure of the 

experiment. 

(3) refine the experimental technique. 

In the cola experiment we could employ 

all three of these methods, but in the 

KCPPE where there are severe limitations 

on how big we can make the sample size, we 

clearly must know how to reorganize and 

refine the experiment to avoid the trap of 

proving the null hypothesis. We address 

these issues in Section IV of this paper. 

B. Differences in treatments 

Directly related to the issue of "provingthe 

null hypothesis" is the choice of treatment 

for the experiment. If there is little or no 

difference among treatments, then we can 

hardly expect to have much luck in 

discovering differences among the resulting 

effects. The treatment standard chosen as 

the "control" in the KCPPE was the 

current patrol strategy and level of patrol 

used in the individual beats involved in the 

experiment. Yet we don't know whether 

this "control" level of patrol differs 

markedly across beats, nor whether it is 

high, moderate, or even low relative to the 

levels of patrol that are feasible for a given 

beat area or for police patrol beats more 

generally. 

Kelling et al. (1974) state the aim of the 

KCPPE as follows: 

In its ultimate design the project would be a rig- orous and systematic attempt to test the out- comes of different patrol strategies and 

ultimately could lead to cost-benefit analyses of 

varied strategies to determine the most efficient 

methods of undertaking patrol. It was likewise 

felt that the preventive patrol experiment would 

help to maintain a climate of innovation and 

self-evaluation, not only on the part of the 

department as a whole but alsoamong individual 

officers. The task force and the Police Foundation realized that since the effectiveness of rou- tine preventive patrol was not self-evident and 

because the capacity to deal with crime is a cen- tral police function, the preventive patrol experiment would fill a real professional need heretofore not addressed by other police agencies. 

The notion of preventive patrol in this 

description is really a "black box,"and the 

problem for the experimenter is that it is 

hard to manipulate such a "black box." As 

Riecken and Boruch (1974) note: 

A specified treatment allows a much more powerful experimental test than does a "black box." 

Furthermore, specifying treatments helps to 

achieve comparability between different experimental sites. ..when an experimental treatment 

is repeated (replicated) it should be kept the same or deliberately and systematically altered, 

rather than being allowed to vary haphazardly. 

What was actually manipulated in the 

KCPPE was some combination of changes 

in manpower, the deployment of manpower, and visibility. Each of these variables 

contributes in a partially undefined way to 

the level of activity in each experimental 

unit, and then the level of activity somehow 

affects the "black box" of prevention. 

Some of the experimental areas were to 

continue with the same manpower levels, 

the same deployment, and the same visibility as before. This was intended to keep 

constant the level of activity in these "control" areas. In a second group of areas the 

manpower was doubled (very roughly), but 

the deployment of manpower was to be no 

different from before. The resulting increase in activity leads to the label of "proactive" for these areas. In the third group of 

experimental areas, the level of manpower 

was left the same, but deployment was 

manipulated. Some of the activities 

associated with the "controls" were eliminated from these areas, and thus we label 

the activity as "reactive." These manipulations of treatment variables leave us with 

the three patrol strategies of the KCPPE. 

The "reactive"and "proactive" patrol strategies appear on the surface to differ 

markedly from the control strategy, but is 

this in fact the case? Routine preventive 

patrol is carried out during an officer's 

noncommitted time, but only 60 percent of 

observed time in the experimental area turned out to actually be noncommitted, 

and only a fraction of the noncommitted 

time is used for activities that might be 

labelled preventive patrol. The uses of 

noncommitted time by officers do not seem 

to vary very much for officers assigned to 

the beats with the three different levels of 

preventive patrol. Since calls for service 

and other routine uses of committed time 

were treated in a similar fashion in all 

experimental beats, the differences among 

the levels of treatment are not nearly as 

great as they appear to be from the initial 

experimental description. Moreover, officers on reactive beats used their preventive 

patrol time either on the perimeter of their 

own beats or in patrolling proactive beats 

to compensate for manpower shortages. 

The amount of time spent on the beat 

perimeters in reactive areas is not given, 

but it should have been carefully assessed 

due to the shape and relatively small size of 

several of the beats. Finally, officers often 

cross beat boundaries in response to calls 

for service. Since there are more officers on 

patrol in the proactive beats, they are more 

likely to be free to cross into reactive or 

control beats in response to service calls 

than the other way around. Finally, as 

Davis and Knowles (1975) note, specialized 

units (helicopters, K-9 units, etc.) were 

deployed independently of the preventive 

patrol experiment at a level consistent with 

activity in the preceding year. 

There is a set of incident types defined by 

Kelling et al. as part of routine preventive 

patrol: traffic violations, building checks, 

car checks, and pedestrian checks. These 

routine patrol incidents are presented by 

treatment group in Table 111-5A of Kelling, 

et al. (1974, p. 47). We have recategorized 

these data to assess more easily treatment 

differences. If there were no differences in 

the levels of preventive patrol across beat 

type we would expect each of the three sets 

of treatment areas to have roughly 33.33 

percent of the routine preventive patrol 

incidents. The 1972 data (collected from 

January through September) are reasonably compatible with thisexpectation, with 

percentages varying from a low of 28.97 
percent to a high of 38.69 percent but with 

most near 33 percent. The 1973 data (also 

January through September), in which we 

would expect the proactive beats to have a 

considerably larger share of the incidents 

and the reactive beats a considerably 

smaller share, present a somewhat different 

picture. The proactive beats in 1973 had 43 

percent of the car checks, 53 percent of the 

pedestrian checks, and close tq 33 percent 

of both traffic violations and building 

checks as opposed to 38, 39, 35, and 34 

percent, respectively, in these categories in 

1972. On the other hand, the reactive beats 

in 1973 had 26 percent of the car checks, 24 

percent of the pedestrian checks, 28 percent 

of the traffic violations, and 28 percent of 

the building checks. These should be 

compared with figures from 1972 of 33,32, 

32, and 37 percent, respectively. The 

control beats were much more stable for 

1972 and 1973 except that pedestrian 

checks dropped from 29 to 24 percent and 

car checks increased from 29 to 37 percent. 

There do appear to be differences in the 

relative proportions of routine preventive 

patrol incidents across treatment areas, but 

the differences are not all that big. What is 

even more troubleso,me is that the number 

of patrol-initiated events that took place in 

the "reactive" areas actually increased from 

1972 to 1973. Although the proportion of 

car checks out of the total number that 

took place in the reactive areas decreased 

from 33 to 26 percent, car checks still 

comprised 45 percent of all patrol-initiated 

activities in 1973 data, whereas they 

comprised less than 36 percent of the 

activities for the comparable period of time 

in 1972. Thus there is some question as to 

what the experimental conditions were and 

how they were maintained. Larson (1976) 

discusses this point in greater detail. 

The figures in the preceding paragraph 

may tend to overstate the treatment differences. To see this it is important to note 

that, unlike many other cities where manpower is scheduled over the day according 

to anticipated police activities, Kansas City 

attempts to equalize its manpower over 24- 

hour periods by allocating the same number of officers to each of the three 8- 

hour watches. Thus most preventive patrol 

activity occurs in the midnight to 8 a.m. 

watch, and the least in the peak workload 

watch from 4 p.m. to midnight. When these 

activities are examined on a day by beat by 

watch basis we find that we are faced with a 

low productivity situation, where big 

treatment changes may be required to 

increase or decrease productivity. Since the 

average number of patrol-initiated activities 

is about one per day per beat per watch, 

how much of an effect can we expect from 

the supposed elimination of preventive 

patrol from the reactive areas and the 

doubling of manpower, which likely 

produces far less than two per day per beat 

per watch? In fact, the biggest source of 

variation in patrol-initiated activities may 

well be among watches within beat, rather 

than among treatment areas. 

C. Treatment inlplementation: 

What was measured.? 

Kelling et al. (1974) seem to have 

abstracted from the literature on patrol 

strategies the assumption that visibility is 

the main factor underlying patrol variations 

and that visibility impact on the crime rate 

might be mediated by changes in "fear of 

apprehension on the part of crimina1s"and 

"police response time" (see page xvii). The 

extent to which differences in treatment led 

to differences in actual visibility is thus 

crucial. The KCPPE used no direct 

measurement of visibility anywhere in the 

study and, while some attempt was made to 

measure response time, the data were 

scanty and not very reliable. Kelling et al. 

(1974) note that there was no consequential 

difference in response time to calls for the 

three areas based on the KCPPE measurements, but Larson (1976), using a simple 

"back-of-theenvelope" operations research 

model, has shown that, for the experimental 

design used, the expected travel time for 

cars in reactive beats would not increase 

very much. Since the experimental units 

were beat areas but what was manipulated 

were beat cars, it is unfortunate that any 

potentially useful information on reaction 

time is recorded by car rather than by beat 

area. 

Let us return to the issue of visibility. 

Crimes where offenders are in private 

places are not accessible to the police for 

prevention efforts, and the offenders who 

commit these crimes are not affected by the 

visibility of police cars. Only street crime 

may be affected and, even in the case of 

purse snatchings and auto theft, visibility 

can aid the offender committing a crime if 

the visibility is fairly predictable. Because 

there was no direct measurement of visibility we must try to infer the amount of visibility associated with each of the three 

"levels of patrol." Using another "back-ofthe-envelope" model, Larson (1976) estimates that the average frequency of preventive patrol passings in the control areas 

in 0.164 passes per hour or roughly one 

every 6 hours. Thus he notes that 

preventive patrol as usual in the experimentaI zone is not very much preventive 

patrol. Even if doubling the number of cars 

in the proactive areas doubles the number 

of times a randomly chosen spot is passed 

in a fixed period of time, this is still only 

once every 3 hours. Larson notes that the 

range of preventive patrol coverages in the 

KCPPE is considerably less than that for 

many other U.S. cities on a typical day, 

thus calling into question how useful the 

Kansas City results would be for other 

cities. 

In summary, there are few (if any) direct 

measures of treatment conditions in the 

KCPPE, and those measurements that are 

available tend to point toward minimal 

differences in treatment effects across the 

three types of treatment. 

D. Manipulating manpower 

versus patrol strategy 

The Kelling et al. report on the KCPPE 

continually speaks of experimenting with 

police patrol strategies, but as we noted 

earlier the experiment itself deals only with 

the manpower levels for the proactive 

treatment and with one particular strategy, 

i:e., reducing preventive patrol for the 

reactive treatment. But manipulating what 

officers actually do while on patrol may 

well have as great an effect on the 

commission of crimes in an area as the 

manpower level of the patrol. For example, 

"stop and frisk" patrol strategies clearly 

involve more intrusive activities than do 

routine patrol strategies. By manipulating 

both manpower and patrol strategy we 

might produce alternatives to routine 

preventive patrol at current manpower 

levels, the effects of which are detectable. It 

is, of course, much easier for us to reach 

this conclusion after examining the KCPPE 

and its results than it would have been 

before it was carried out. 
Whenever manpower is highly inefficient, 

or has low productivity relative to what it 

might have, increasing the number of 

workers will have relatively little impact on 

reducing the levels of crime. If a police 

officer makes only one car check a day 

when he could easily make 10, then doubling the manpower (assuming a constant 

ratio of manpower to activity) would produce only 2 per day but changing the patrol 

strategy could produce 5 times that 

number. In short, when we are faced, as we 

are in Kansas City, with very little preventive patrol strategy other than riding and 

sitting around, we can't expect changes in 

manpower to produce very much. Thus 

leaving the ordinary conditions of productivity constant, we must ask whether 

changes in manpower will make much 

difference. To the extent that one can 

increase levels of output per man by 

changes in patrol strategy, one can measure 

the effect of the strategy. An interesting 

question is whether changes in strategy can 

produce more effect than changes in 

manpower. Up to some point, there can be 

enormous gain by changes in strategy, and 

similarly only to some given pointusually spoken of as a saturation pointcan changes in manpower have an effect. 

Under many conditions, tripling, etc., 

manpower does not have the expected multiplicative effect. 

In an experiment like the KCPPE, whether 

we try to manipulate manpower, patrol 

strategy, or both should depend upon the 

level of effect expected per man for a given 

strategy relative to what might be achieved 

by increasing output per man. There is little 

reason, we believe, to increase police 

manpower when the current manpower is 

used so inefficiently relative to any strategy. The problem is complicated by the fact 

that events are not uniformly distributed in 

time so that manpower will have less effect 

at some times than others and ceiling 

effects are quickly reached. Between 2 and 

4 a.m., there may be very few people to 

interrogate and very few cars to check in 

most beats of even a very large city. Thus 

strategy changes have different limits for 

different times. We frankly don't know 

how the experiment we propose in Section 

IV (or any other experiment) can take these 

difficulties into account, particularly because 

most strategies attempt to affect the 

offending populations, and we know so 

little about police interactions with such 

populations. 

E. Strategies in adjacent beats 

As we noted above, officers are dispatched 

across beat boundaries in answer to calls 

for service. With more manpower on 

routine preventive patrol in proactive 

areas, officers from proactive beats are 

much more likely to be able to answer calls 

in another beat than are officers from 

reactive or even control beats. Officers in 

one beat may in fact feel compelled to" help 

out" their colleagues in adjacent reactive 

beats and thus negate the intended effects 

of the experiment. Since controlling the 

dispatch of police cars is a near-impossible 

task, care must be taken in allocating 

treatments to beats to allow a measure of 

control relating to effective treatment 

differences in adjacent beats. 

In this regard, we should reexamine the 

schematic representation of the 15-beat 

experimental area, reproduced here as Figure 1. The striking feature of the layout is 

the placement of the 5 reactive beats in the 

4 corners and in the middle. Proactive and 

control beats intervene between every pair 

of reactive beats, and the only 4 beats with 

2 sides adjacent to areas not in the experiment are all reactive. The probability that 

such an allocation of treatments to beats 

would happen by chance is quite small 

indeed.' In fact, as the authors of the 

KCPPE note in the Summary Report: 

"The geographical distribution of beats 

avoided clustering reactive beats together 

or at an unacceptable distance from proactive beats. Such clustering could have 

resulted in lowered [sic] response times in 

the reactive beats." The consequences of 

the geographical distribution are far more 

distressing, both because they indicate a 

lack of random assignment and because of 

the interactive effects described above. The 

arrangement of beats is of even greater 

concern once we realize the potential significance of a beat's being on the edge of the 

'In experimental situations such as the KCPPE there 

are several recognizable subsets of possible designs 

which for one reason or another may seem striking. 

While each of these designs might occur with small 

probability asa result of randomization. the probability of chosing a design coresponding to one of the 

recogni7able subsets is substantially larger. 

Figure 1. 

Schematic representation of the 

15-beat experimental area 

R . C CR 

-


P C R C 

-

P

P -

P 

R R 

C 

P = Proact~ve 


C = Control 


R = Reactwe 


- experimental area. The South Patrol 

Division is bordered at the west by Kansas 

City, Kansas (which is under different 

police jurisdiction), and on east and south 

by yet additional suburban Missouri police 

jurisdictions. Because police rarely if ever 

cross jurisdictional lines, let alone state 

lines, the geographical arrangement of 

beats in the KCPPE leads one to wonder 

how the results might have turned out had 

a different arrangement been used, especially one that controlled for what we 

might label "border" effects. 

F. Random assignment of treatments 

The layout of the experimental area and 

the discussions of it in Kelling et al. (1974) 

raise considerable doubt whether randomization was used at all in the assignment of 

treatments to beats. Is this a serious 

matter? We believe strongly that it is. The 

difficulties resulting from a nonrandomized field trial are many, but as Gilbert, 

Light, and Mosteller (1975) note, "The key 

problem is that the effect of the treatment is 

not distinctive in all cases, so that the 

treatment cannot be proved to have caused 

the effect of interest. Selection effects and 

variability of previous experience have 

often led to biases and misinterpretations." 

Now it is true that by making certain 

assumptions regarding models and the 

nature of the experimental variability we 

can hope to surmount the obstacles posed 

by the lack of proper randomization in an 

experiment or controlled field trial. Yet 

this hope all too often remains just that, 
and the only sure way to be able to make 

causal statements after we complete an 

experiment is to randomize at some stage 

of the allocation of treatments to units. The 

nonrandomized controlled field trial can 

be an effective evaluation device, but 

primarily in the presence of what Gilbert, 

Light, and Mosteller call "slam-bang 

effects," hardly a phrase that can be used in 

describing the results of the KCPPE. 

It may well be argued that a simple random 

assignment of treatments to beats in the 

KCPPE would have been inappropriate. 

But experimental designs that balance the 

allocation of treatments, and yet also 

involve some form of random assignment, 

are available. 

IV. Designing a new patrol 

strategy experiment 

It is possible to design a new experiment to 

examine alternative police patrol strategies 

in the spirit of the KCPPE that would overcome the pitfalls elaborated upon in the 

preceding section, although the task is not 

at all an easy one. The difficulty comes 

when we attempt to control for a variety of 

different sources of variability. Although 

such control in principle increases the efficiency of an experiment, we must retain 

sufficient degrees of freedom for the error 

term in order to keep the power against 

interesting alternative hypotheses high. 

Because the number of police beats in a 

given city is never very large (e.g., 69 beats 

in Kansas City, Missouri, and only 24 beats 

in Minneapolis, Minnesota), we need to 

strike a balance between the control of 

variability and the estimation of residual 

error. 

In this section we describe an experimental 

design for a new patrol strategy field trial 

and several variants of added or diminished 

complexity. The basic design described 

involves 108 beats and thus cannot be 

implemented in any but the largest cities in 

the United States. By assuming theabsence 

of all interaction effects we can reduce the 

required number of beats to 54. By utilizing 

natural boundaries such as the Missouri 

River and Missouri-Kansas state boundary 

line, we can cut these requirements to 70 

beats for the full experiment and 28 for the 

reduced one (assuming completely regular 

beat sizes and shapes). 

For those not familiar with the sophisticated details of the design of statistical 

experiments, the experiment described 

here may seem so complex that we have no 

hope of using it to detect interesting results 

that we might have discovered had we only 

tried to manipulate one factor and answer 

one question. The distinguished statistician, Sir R. A. Fisher (1926), once 

pointed out that he believed exactly the 

opposite to be true: 

In most experiments.. .the comparisons involving single factors. ..are of far higher interest and 

practical importance than the much more 

numerous possible comparisons involving several factors. This circumstance, through a 

process of reasoning.. .leads to the remarkable 

consequence that large and complex experiments have a much higher efficiency than simple 

ones. No aphorism is more frequently repeated 

in connection with field trials, than that we must 

ask Nature few questions, or ideally, one question, at a time. The writer is convinced that this 

view is wholly mistaken. Nature, he suggests, 

will best respond to a logical and carefully 

thought out questionnaire; indeed, if we ask her 

a single question, she will often refuse to answer 

until some other topic has been discussed. 

A. Treatments 

In place of simply varying the manpower 

level of routine preventive police patrol, we 

propose to vary the actual patrol activities. 

We do so in part because of what we have 

learned about varying manpower from the 

KCPPE. 

Before suggesting specific treatments for 

our proposed experiment, we offer a list of 

treatments built upon the idea of testing 

alternative police patrol strategies and 

tactics: 

(1) Information processing patrol strategies. These strategies rest on the assumption that sharing information gathered in 

police patrol among the patrol officers 

policing a common area will reduce crime 

by increasing the risk of apprehension of 

offenders. 

Tactic I: Information oflicer coordination of beat patrol. This system, pioneered 

in England, rests on the principal that each 

beat officer shares information on crime 

and offenders in his beat with an 

information officer who also gathers information from the wider criminal justice 

system. This information is processed and 

serves to direct the patrol activities of each 

beat officer with a view to increasing apprehension of offenders or to increasing 

their risk of being caught and thus reducing 

their level of offending. 

Tactic 11: Neighborhood team policing. 

This tactic emphasizes the creation of a 

team of officers who regularly patrol a 

given territory in which they develop a 

close relationship with potential victims 

and a knowledge of potential offenders. 

(Bloch & Bell 1976; Schwartz and Clarren 

1977; Sherman et al. 1973) 

(2) Environmental intervention strategies. These strategies involve active patrol 

intervention in the physical and social 

environment of patrol areas or in the activities of citizens as they move about the area. 

Tactic I: Stop & Frisk. This tactic was 

examiiied in patrol areas of Chicago, 

Boston, and Washington, D.C., in studies 

by the National Crime Commission in 

1966. The assumption is that the identification of potential offenders, particularly 

those who possess weapons, reduces the 

risk of their use in crimes. (Reiss 1967) 

Tactic 11: Stop and interrogate (question). This tactic'assumes that questioning 

susvicious individuals deters votential 

offinders. (Boydstun 1975) 

Tactic 111: Directed deterrent patrol. 

This includes a variety of tactics designed 

to specify the kind of activity patrol will 

undertake when assigned to preventive 

patrol, e.g., identify vehicles parked in an 

area, or check the security status of residences or buildings. (Larson 1972; Tien et 

al. 1976) 

Tactic IV: Tactical squads. There is a 

large number of possible types of tactical 

squads whose tactics include proactive 

policing. The location-oriented patrol 

(LOP) and perpetrator-oriented patrol 

(POP) tactics attempted in Kansas City 

following the completion of the KCPPE 

are examples (Pate et al. 1976). 

(3) Visibility strategies. These strategies 

are based on the presumption that degree 

of visibility of police patrol affects the rate - of offending in an area. The tactics appear 

superficially to be contradictory, with 

unmarked cars as well as marked cars 

presumed to have effects increasing the 

apprehension of offenders. 
Tactic I: Unmarked palrol cars. This 

tactic is based on the assumption that large 

manpower allocated to unmarked patrol 

cars increases the risk of apprehension of 

offenders committing crimes. 

Tactic 11: Reactive patrol. Here visibility results solely from reactive dispatches 

into an area in response to complaints. This 

is a low visibility condition. 

Tactic 'I1: Foot This tactic is 

based on the assumption that foot patrol 

officers have knowledge of their beat and 

how to secure it so as to reduce the risk of 

victimization by crime and the apprehension of offenders. 

Tactic High visibility. This tactic 

assumes that offenders are deterred by the 

open presence of police officers, either on 

patrol or functioning in some other 

fashion. 

(4) Crime-specifc strategies. These strategies are based on the assumption that no 

patrol strategy is effectiveagainst all crimes 

and that the greatest deterrent and 

apprehension effects arise from tactics that 

are undertaken for a specific type of crime. 

Among those that have been tried are: 

Tactic I: Decoy squads for street 

robbery. A police team with one or more 

members serves as decoys by representing 

potential victims of street robbery. This is 

intended to increase the apprehension of 

career street robbers. 

Tactic 11: Operation barrier for apprehending robbers. This tactic dispatches 

patrol to intercept robbers in flight and is 

designed especially for commercial and 

street robbers. 

Tactic 111: Identification tactics: Various tactics of surveillance including 

technological surveillance (e.g., burglar 

alarm systems linked to patrol operations) 

are used to increase the apprehension of 

criminals by police on patrol. 

(5) Patrol investigation strategy. This 

Strategy assumes that police patrol can 

increase the apprehension rate as well as 

the effectiveness of detective investigation 

if the police on patrol immediately undertake some investigation of the crime rather 

than leaving investigation primarily to the 

detective division. 

Tactic I: Team patrol to manage investigations. This tactic includes the assignment 

of detectives to patrol teams (Bloch and 

Bell 1976). 

Tactic 11: Combining detective investigation with patrol function. Each patrol 

officer does substantial detective investigation as part of routine patrol. 

I 

The ex~erimenter will find that these strategies and the tactics related to themare not 

readily separable from one another. For 

example, it is no simple matter to separate 

foot patrol from the special activities undertaken by police officers on foot patrol that occur in other strategies and tactics. 

Were sample size not a severe and 

overriding problem in the present situation, we would most likely propose a 

factorial or fractional factorial structure 

for treatments aimed at measuring the 

effects of three or more strategies and their 

interactions. Since the available number of 

police beat areas is so small, and for purposes of comparability with the KCPPE, 

we have decided to consider only the 

following threeUtreatments." werecognize 

that the proposed interventions require 

changes in police behavior that may be very 

difficult to achieve. 

(A) A search patrol strategy, involving 

high visibility (see Strategy 3, Tactic IV) of 

the participating police officers and intrusive forms of patrol involving field interrogation of suspicious individuals and 

other forms of environmental intervention 

(see Strategy 2, Tactics I and 11). 

(B) A basic visibility patrol strategy, 

involving a standard level of routine preventive patrol. 

(C) A reactive no-patrol strategy (see 

Strategy 3, Tactic II), utilizing police officers wherever possible to handle complaints related to particular types of crime 

via scheduled appointments and in unmarked patrol cars (see Strategy 3, Tactic 

1). 

If the effects of these treatments do differ, 

and if we assume that there are no interactive effects of visibility and interrogation 

(i.e., they are additive), then the differences 

between beats with treatments B and C will 

be a measure of the effects of the visibility 

component of patrol, and the differences 

between beats with treatments A and B will 

be primarily a measure of the effects of 

interrogation. If the experiment we propose 

here is successful and detects sizeable 

differences in the effects of treatments, then 

subsequent experiments might explore the 

interrogation versus visibility structure in 

further detail. 

B. Do we monitor treatments? 

We propose to monitor various aspects of 

police activities at the beat level and to 

collect basic response information similar 

to that in the KCPPE. The purpose of 

monitoring police activities is to ensure 

that there is a true difference in treatments, 

and thus we are interested in havingadirect 

measure of police car visibility. One way to 

measure visibility is to use, at a variety of 

locations, counter devices that candistinguish 

among patrol cars. Such devices would 

also provide measures of the presence of 

cars from other beats, e.g., in answer to 

calls for service. 

An (expensive) alternative to counter 

systems is an automatic vehicle monitoring 

system such as the FLAIR (Fleet Location 

and Information Reporting) system cur- rently being implemented in St. Louis on a trial basis. The St. Louis FLAIR system 

a form 

guidance" technique with 

Puter tracking to the location of 

each of 25 patrol cars within what is 

be an average accuracy 

feet. Such a system would not only allow 

for the direct measurement of but 

it would also allow for better control of 

police operations such as dispatching. 

we are also interested in monitoring the 

amount of interrogation, especially in 

beats using the search patrol strategy. We 

suggest the filling out of punched cards by 

officers for each field interrogation or car 

In addition to the basic response data used 

in the ~cpp~, such as UCR and 

victimization data and citizen response 

data, we suggest the collection of additional information such as weapons 

production. What we are seeking here is the 

offender protection potential of each 

strategy. For example, in car checks, we 

would like to know how often we produce a 

hot car, a wanted person on warrants, etc. 

~f we increase that strategy, do we increase 

the numbers of such events? For searches 

of the person, we would like to know how 

often we produce a weapon, burglary tools, 

narcotics, etc. In short, what we want is 

direct evidence from the activity itself. Do 

searches produce evidence of a direct 

criminal sort, e.g., burglary tools, or of a 

more indirect sort, such as weapons since 

they could be for self-protection, stolen 

goods, persons wanted on warrants, etc.? 

We would also want to know whether 

weapons production has any effect on 

particular kinds of crime rates. Indeed, we 

should expect that increased productivity 
of weapons 'taken might be related to 

reductions in carrying weapons over time. 

We also would record separate measurements by "beat-watch." Since there are 

three standard watches for each beat this 

would give us a trivariate response variable. We could then examine differences 

among watches within beats, as well as differences among beats within watch. 

C. How long an experiment? 

The KCPPE ran for a I-year time period. 

Because of the important seasonal variation 

in the levels of various types of crimes and 

in exposure, the KCPPE could only use 

one level of preventive patrol in each beat. 

We propose an experiment that will run for 

3 years. This expanded time frame will (1) 

allow for the use of all three patrol 

strategies in each beat for a full year, (2) 

permit the assessment of effects beyond 

those considered in the KCPPE, and (3) 

provide an acceptable number of degrees of 

freedom for an estimate of exverimental 

error. This approach in effect ailows each 

beat to serve as its own control, and thus 

enables us to control more accurately for 

beat-to-beat variations. 

The time period of I year per treatment is 

dictated by the need to accumulate sufficient data by beat-watch of rare or low productivity events. Such a period also 

removes the need to adjust directly for seasonal effects, and allows police officers 

sufficient time to adapt to different patrol 

strategies. If such surveys were not needed 

to provide various response measures, 

more interesting and efficient experimental 

designs could be proposed. For example, if 

one were to use a time period of 4 months 

per treatment, one could apply each 

treatment twice to each beat (so the length 

of the experiment becomes 2 years), thus 

increasing substantially the degrees of 

freedom associated with the estimate of 

experimental error. Such a plan would 

assume that the effects of treatment 

changes could be assessed after only 4 

months. Moreover, in this 2-year experiment each treatment would not be applied 

to each beat for each of the 4 seasons. 

Hawthorne effects, resulting from the 

seemingly continuous changes in treatment, might also result. 

Although 3 years is a very long period of 

time for the implementation of a social 

experiment, we feel the advantages here 

outweigh the potential hazards. 

D. The basic crossover designformat 

The basic experimental design that we 

propose has two key features: 

(I) Different treatments are applied to 

the same experimental unit during different periods, and this results in a crossover 

or changeover design (see Cochran and 

Cox 1957). 

(2) The use of primary and secondary 

experimental units, with the secondary 

units providing a double insulation between "adjacent" primary units. 

The initial experiment analysis is aimed 

at the consideration of the primary units, 

although the effects of the treatments 

applied to the secondary units are taken 

into account. Depending on the results of 

this initial analysis, subsequent analyses 

may make use of the secondary units in 

addition to the primary ones. The units of 

analysis always remain the individual 

police beats. 

We assume that all beats are square and of 

the same size. While this is far from true in 

practice, we expect that modest variations 

in size and shape will not seriously affect 

the implementation of the design. 

We begin by dividing the beats into 3 x 3 

blocks of 9. The basic configuration of 

beats within blocks has the primary unit 

surrounded by 8 secondary units as shown 

in Figure 2. 

For any given experimental period we 

intend to use the same treatment (i.e., 

patrol strategy) in all 8 secondary beats 

within a block. Because our initial analyses 

will use data from only the primary beats, it 

may seem extremely wasteful to use up a 

total of 9 beats with potential information 

to yield only the primary beat. We do so in 

order to be able to measure the direct 

effects of strategies in the secondary beats 

on the primary beat which they surround. 

The inability to make such measurement 

appears to have been a serious problem in 

the KCPPE. If these effects involving 

adjacent beats are negligible, then we can 

still carry out subsequent analyses using 

measurements on all beats. 

In the unlikely event that an effect is more 

likely to be observed in secondary rather 

than in primary beat units, the analysis 

could be redone taking into account the 

units surrounding each secondary unit. 

Figure 2. 

Primary un~t= rn 

Secondaty unit = 

-

The reason that this possibility exists is that 

each beat contains a somewhat different 

mix of commercial and residential properties, 

and we expect to find different crimes at 

different times of the day associated with 

the two types of properties. For example, 

the southwest part of the Southern Patrol 

Division in Kansas City consists primarily 

of upper middle class residential properties, 

but one beat in this area contains a modern 

shopping area, and we would expect the 

mix of crimes associated with this beat to 

differ from the other beats nearby. At some 

point in the analysis the combination of 

commercial and residential properties 

within beats should be examined as a 

possible concomitant variable. 

The 3-year experimental time frame is 

divided into three consecutive I-year periods, and for each primary beat we use a 

different patrol strategy during each period. This is the crossover feature referred to 

above, and each primary beat serves as its 

own control. We also vary the use of the 

three patrol strategies in the secondary 

beats within each block in a similar 

fashion, so that within each block all 8 

secondary beats first use one strategy, then 

a second, and finally a third. Thus there are 

36 possible patrol strategy combinations 

for a given block of 9 beats, since there are 6 

possible orderings of the strategies for the 

primary beats, and for each of these 6 ordering~there are 6 possible orderings of the 

strategies for the secondary beats. This sugests an experiment involving 36 blocks or a 

total of 36 x 9 = 324 beats, clearly an 

impossibility! 
By carefully balancing treatment combinations in sets of blocks we can design experiments involving 6, 9, or 12 blocks of 

interest. This leads us to variants on sets of 

Graeco-Latin squares treated in the form 

of crossover designs. Alternatively we can 

choose a set of treatment combinations at 

random from the 36 possible ones. We 

explore both of these possibilities below. 

To keep our descriptions of designs 


compact, henceforth we use the following 


shorthand notation for patrol strategies. 


Capital Latin letters refer to strategies used 


in the primary beats within a block, and 


Greek letters refer to strategies used in the 


secondary beats: 


A(a) = Search strategy. 


B(P) = Visibility strategy. 


C(y) = Reactive no-patrol strategy. 


We denote the three successive I-year time 

periods as Tl, T?, and T3, respectively. 

For all the designs we discuss below, we are 

interested in effects due to: 

(1) blocks of beats. 

(2) time period. 

(3) patrol strategies in primary units. 

(4) patrol strategies in adjacent secondary 

units. 

We would also like to be able to test for the 

presence of various interaction effects, 

such as: 

(5) primary by secondary patrol strategies. 

(6) time by patrol strategy (either in the 

form of residual or carryover effects), for 

both primary and secondary beats. 

A residual effect during a particular time 

period depends only on the treatment 

(strategy) used in the preceding period. A 

carryover effect, as used here, depends on 

both the treatment in the preceding period 

and the treatment in the present one. Thus 

the "carryover" model allows for different 

effects resulting from the preceding treatment, when the transition is from search to 

control or from search to reactive, whereas 

the model based on residual effects forces 

the effect of the preceding treatment to be 

the same in both cases. 

Of all the effects listed here the one we 

consider to be least substantial is that of the 

interaction between the patrol strategy in 

the primary beat and the patrol strategy in 

the secondary beat. If we were forced to 

choose between including this interaction 

in our model and design or achieving 

superior experimental balance with additional degrees of freedom for estimating 

the error term, we would opt for the latter. 

This is because the magnitude of detectable 

effects suggested by all previous controlled 

studies is not that great, and the physical 

(as opposed to parametric) interactive 

effect of secondary units on adjacent primacy units is already taken into account by 

the model. The next least important among 

the effects would seem to be residual effects 

due to secondary-beat strategies. 

The model that goes with this experimental 

structure assumes that each response variable (or some function of it, like the logarithm or log-odds in the case of proportions) is the sum of effects attributable to 

each source. Thus if we are looking at a 

beat with primary strategy A and secondary strategy P during period Tz,when strategies C and a were used in TI,the model 

with residual effects postulates that the 

response variate 

= (beat effect) 

+ (main effect due to period T?) 

+ (main effect due to A) 

+ (main effect due to /3) 

+ (residual effect due to C) 

+ (residual effect due to a) 

+ (interaction effect due to A x p) 

+ (random error). 

If we use carryover effects, then in this 

model we replace the residual effect due to 

C and the residual effect due to a by a carryover effect of C preceding A and a 

carryover effect of a preceding P. 

Note that the model includes a term 

labelled "beat effect." All beats do not start 

from the same level of the response variable, e.g., beats differ in their rate of automobile theft. The crossover design described here uses each beat as its own 

control, and attempts to remove the initial 

differences among beats by incorporating 

an additive effect due to beats in the model. 

The fact that beats with low crime productivity would not be expected to respond to 

particular treatments in the same "additive 

way" as beats with high crime productivity 

suggests that when crime rates are used as 

response variables, the additive model is 

more appropriate for the logarithm of the 

crime rate. The use of such transformations 

is standard practice in modern statistical 

data analysis. 

Most crossover experimental designs that 

assume the presence of residual effects do 

so only for the actual time frame of the 

experiment, i.e., they assume that there are 

no residual effects for period TI.Although 

the discussion below is based on such an 

assumption, it would seem to be inappropriate in the proposed experiment. In particular, we might expect to find a residual 

effect during TI in the beat with primary 

strategy C and secondary strategy y, since 

prior to the experiment all beats supposedly are using the current preventive patrol 

strategy (i.e., B and 0). The analyses described below can take such effects into 

account but the modifications result in 

some additional nonorthogonalities in the 

associated analysis of variance breakdowns. 

E. Random crossover designs 

In order to be able to test for all of the 

effects listed above we require a minimum 

of 9 or 10 blocks (depending on whether we 

use residual or carryover effects). To 

ensure a sufficient number of degrees of 

freedom for error we probably need a 

minimum of 12 blocks unless we are 

prepared to assume the absence of 

interaction effects. 

In this subsection we describe two 

examples of "random crossover" designs, 

one with 12 blocks that can be used to get 

tests for all of the different effects and a 

second one with 6 blocks that can be used 

to get tests for the main effects. 

One possible random 12-block design can 

be described as follows: 

Block 

1 

2 

3 

4 

5 

6 

7 

8 

9 

10 

11 

12 
-

Table 1. ANOVA layout for 12-block 

cross-over design with carry-over 

effects 

Source -df

Blocks (beats) 11 

Time 2 

Primary strategy 2 

Secondary strategy 2 

Primary x secondary 4 

Primary carry-over 3 

Secondary carry-over 3 

Error -
8

Total 35 

J 

Table 2. ANOVA layout for 12-block 

cross-over design with residual effects 

Source -
df

Blocks (beats) 11 

Time 2 

Primary strategy 2 

Secondary strategy 2 

Primary x secondary 4 

Primary residual 2 

Secondary residual 2 

Error -
10

Total 35 

Table 3. ANOVA layout for 6-block 

random cross-over design 

Source -df

Blocks (beats) 5 

Time 2 

Primary strategy 2 

Secondary strategy 2 

Error -
6

Total 17 

Table 4. 

-

Block T1 -T2 -T3 

1 

2 

Aa 

BY 

BP 

Ca :J 

3 CP AT Bci 

4 Ba AT ‘3 

5 Aa 

6 A Ca 

7 AY BP ca 

8 Ba CY AP 

9 CP Aff BY 

10 Aa CP BY 

11 BP AT ca 

12 CY Ba 43 

As indicated above, each patrol strategy is 

used exactly once for the primary unit in 

each block and exactly once for,the secondary units. Because we randomly selected 12 

of 36 strategy combinations Aappears only 

twice in TI,while B and C appear 5 times 

each. This lack of balance leads to a nonorthogonal analysis of variance where the 

ordering of the effects to be tested may 

make a difference. Of course other random 

crossover designs may be better than this 

one, while many others will definitely be 

worse. 

All 6 effects in the original list in Section 

IV-D are estimable with this particular 

random design, and there is not too great a 

disparity in the precision of the estimates if 

we use a standard Analysis of Variance 

(ANOVA) model meeting the usual restrictions on parameters. Table I lists the effects 

and the associated degrees of freedom for 

the model with carryover effects and Table 

2 lists these for the model with residual 

effects. 

As we remarked in the preceding subsection, modifications in the standard ANOVA 

analyses are required to take into account 

carryover effects from the standard treatment (B and /3) used prior to the experimental period. 

The first 6 blocks'in the preceding design 

can be used to illustrate a 6-block random 

design that can be used to test the four sets 

of main effects. The resulting ANOVA is 

given in Table 3. 

F. Balunced crossover designs 

Rather than trust the estimability of the various 

effects of interest to a random selection of 

12 out of the 36 treatment sequences, we 

can try to prepare a design that balances the 

assignment of treatments to experimental 

units in a crossover experiment. Patterson 

(1952) has given the following list of 7 conditions for balance in a general crossover 

design: 

(1) No treatment occurs in a given 

sequence more than once. 

(2) Each treatment occurs in a given 

time period an equal number of times. 

(3) Every two treatments occur together 

in the same number of sequences. 

(4) Each ordered succession of two 

treatments should occur equally often in 

sequences. 

(5) Every two treatments occur together 

in the same number of curtailed sequences 

formed by omitting the final period. 

(6) In those sequences in which a given 

treatment occurs in the final period, the 

other treatments occur equally often. 

(7) In those sequences in which a given 

treatment occurs in any but the final 

period, each other treatment occurs equally often in the final period. 

These conditions for balance are for crossover designs involving only one type of 

treatment, i.e., only one for the Greek or 

Latin labelled effects used above. Conditions (I), (2), and (3) ensure that main 

effects are estimable, while if both 

conditions (1)-(3) and (4)-(7) are satisfied, 

then both main effects and residual effects 

are guaranteed to be estimable and obtainable in a simple form. Toapply these conditions to the design problem considered 

here, we consider them once for treatments 

assigned to primary beats and a second 

time for treatments assigned to secondary 

beats. As far as we know, this will still not 

necessarily ensure that the primary by 

secondary interaction parameters are estimable, so for any particular balanced design 

satisfying (1)-(7) we must make a special 

check regarding the estimability of these 

parameters. 

The random design described in the previous subsection satisfies conditions (I), (3), 

and (6), but not the, others. Clearly any set 

of sequences built using Graeco-Latin 

squares of the form 

(in which each Greek and Latin letter 

appears only once in each row and column, 

and each Greek letter appears only once 

with each Latin one), must satisfy conditions (1 ), (2), and (3). The design in Table4 

was built with 4 such Graeco-Latin 

squares, and the reader may verify that the 

design satisfies Patterson's 7 conditions for 

both Greek and Latin letters. In this particular design the primary by secondary treatment interaction parameters are also 

estimable. 

The ANOVA layouts for the balanced designs are the same as in Tables 1 and 2 for 

the random design, but the Graeco-Latin 

square structure will make several of the 

sums of squares orthogonal to one another, 

a situation that did not exist for the 

random design. 

The first six sequences in the above design 

(or the last six) may be used by themselves 

to give a balanced design for estimating 

only the main effects as in Table 3. These6- 

block designs have the added feature that 

they allow for the estimation of both primary and secondary residual effects. If we 

choose to break both of these residual sums 

of squares out of the error sum of squares, 

the resulting error sum of squares has only 

2 degrees of freedom, and thus any 

ANOVA tests will have very low power. 
-- -- 

-- -- 

In order to ensure that the analyses we are about to describe are proper, theallocation Table 5. Variances of parameter estimates in the model with residual effects of symbols (both Greekand Latin) to treatments, and sequences to blocks of beat 	 Balanced Random Balanced Random 

must be madeat random (Patterson 1952). Treatments A .07402 .19002 Block B1 .492 .700 A systematic assignment of treatments B .074 .I90 effects B2 .656 .722 

simply will not do. C .076 .I14 B3 .492 .697 

Insulation a .076 .I31 B4 .492 .493 

0 .074 .098 	 B5 .492 .763 

Y .074 .I71 	 B6 .656 .698 G. Comparing the balance Residual A .I72 .333 B7 ,647 1.16 

and random designs treatment B .172 .205 .517 .842 

C .149 .247 B9 .517 .462 

Although there is an aesthetic appeal to the Residual a .I49 .231 B10 .517 .581 

insulation p .I72 ,212 	 B1l .647 .436 balanced design described above, we have Y .I72 .242 B12 .517 .763 

no guarantee that it is in fact superior to the Interaction Aa .241 .483 Time TI .074 .089 

random, unbalanced design. In Tables 5 effects Ap .602 .562 T2 .I86 .070 

AY ,602 .437 	 T3 .I85 .088 and 6 we give the variances associated with Ba .241 .734 

each of the estimated effects in the two 	 .602 .442 

BP .602 .806 complete (12-block) models, the one with Ca By.296 .507 


residual effects and the one with crossover .241 .559 


effects. Each variance is some multiple of CPY .234 .SO6 


the variance, a2, of the random error term. 


In Table 7 we give similar expected 


variances for the two 6-block designs Table 6. Variances of parameter estimates in the model with cross-over effects 

(random and balances) assuming the 

presence of neither residual, carryover, nor 	 Balanced Random Balanced Random 

interaction effects. 	 Treatments A .063a2 .1 4002 Block B1 1.18 .789 

B .063 .I85 effects B2 1.08 1.03 For the 12-block experiment and the model C .056 .I32 B3 1.18 .843 

with residual effects the balanced design Insulation or .056 .I45 Bq ' 1.18 1.22 

seems superior to the random one, except P .063 .lo9 B5 1.18 .921 

Y .063 .I66 	 1.08 .777 _ . for a few primary by secondary interaction Avs B before C! .618 .579 B7 1.08 1.32 

parameters. For the model with carryover A vs C before B .619 653 1.18 .960 

effects, however, the results are less clear. B vs C before A .619 .353 B9 1.18 .881 a vs f3 before y 519 .482 	 B10 1.18 .672 

The balanced design is superior for the or vs y before P .619 .408 	 Bll 1.08 .784 

main effects due to treatments in the p vs y'before a .618 .467 	 812 1.18 .903 

Interaction Aa .741 .594 Time T1 .074 .I17 primary and secondary beats, but other- effects Ap .852 .701 	 T2 .I85 .080 

wise the random design is by and large 2: .852 .489 	 T3 .I85 .090 

.741 .915 superior. All things considered, we prefer 	 .852 .596 

the balanced design. For the 6-block 	 BYP .852 .930

. experiment the balanced design is appar- Ca .296 .606 

CP .741 .751 ently superior again. 	 CY .741 .946 

Further comparison between the designs 

has been carried out in terms of the statisti- (1) Survey and questionnaire data, It would be extremely useful to have data 

cal power of the various tests for effects including results from both community on response time to calls for service. The 

resulting from the ANOVA. The calcula- and commercial surveys regarding victim- KCPPE collected such data through a pair tions are summarized in a series of tables ization and attitudes. of surveys (one of observers and the other 

presented in. the Appendix. The power (2) Interviews with officers and partici- of citizens). If an automatic vehicle monicalculations seem to substantiate the pant observations. toring system such as FLAIR is used to 

superiority of the balanced design and (3) Departmental data such as those on track police vehicles during the experiment 

suggest that we have a very high chance of reported crime, traffic, and arrests. as we propose, then departmental data on detecting most effects that are about the response times would be available for analsize of the standard deviation of the Given the nature of the crossover design ysis. Analysis need not be based on com- random error term in the model. being proposed, carrying out multiple vic- plete data for each time period, but meas- timization surveys seems highly imprac- urements at three points for each condition tical because of the large sample sizes 

H. Response variables to be measured required to get useful information (the (beginning, middle, end) seem desirable. 

The KCPPE used three types of response sample sizes in the KCPPE were clearly The fact that the beginning of one condivariables to assess the effects of different much too small to produce useful informa- tion is the end of another simplifies matters 

patrol strategies: 	 tion). Therefore we do not propose to carry here somewhat. 

out any surveys as part of an effort to Not only do we propose to analyze direct 

directly monitor the ongoing effects of the measures of reported crime and police proexperiment. duction (e.g., arrests) which are part of 
Table 7. Variances of parameter 


estimates in 6-beat design 
 I I 


Balanced Random I --I 

Treatments A .ll 1u2 .233u2 B .I11 .I92 

C .I11 .I25 

Insulation a .lll .215 

.I11 .I31 

I Block 

effects 

y 

B1 

B2 

61 

.I11 

.278 

.278 

.278 

.I92 

.278 

.278 

.278 

Time T1 .lll .I59 

T2 .I11 .I11 


T3 .111 .159 


departmental records, but we would also 

like to have several offender-related 

response measures since we anticipate that 

the treatment tactics will have "deterrent" 

effects on potential offenders. Some 

possibilities are: 

(a) Data on modus operandi for offenses. These are hard to get and will be the 

least sensitive to changes. 

(b) Data on rearrest rates and place of 

occurrence of offense for rearrested 

offenders. 

(c) Data on characteristics of offenders 

for crimes against the person, e.g., changes 

in race, age, and sex of offenders in beats. 

Thus, for example, blacks might commit 

fewer offenses in white areas with an interrogation procedure or juveniles might be a 

smaller proportion of all offenders. 

(d) The ratio of crimes against persons 

to property. This is again a highly indirect 

measure but offenders might shift more to 

crimes of stealth under increased proactivity. On the whole this would be a difficult 

measure to interpret. 

(e) Changes in the population of 

offenders with afirst arrest and in proportion of offenders with a first arrest. Both 

have defects as measures, yet they could be 

affected by proactive tactics. 

(0 Changesin distance between place of 

occurrence of offense and residence of 

offender. If an entire city is used, this 

should not change if resources were 

constant, but they are not. Offenders might 

be more inclined to go greater distances 

where the police have a larger territory to 

cover with increased proactivity. 

The foregoing is a tentative list of possible 

response variables to be measured and 

analyzed. Considerably more work is 

required to refine this part of the proposal. 

In Section 111-E we discussed problems in 

the KCPPE which resulted from some 

beats in the experimental area being on the 

boundaries of the city of Kansas City, 

Missouri. By making a few plausible 

assumptions, we can turn what was 

formerly a disadvantage into a benefit and, 

in the process, cut down on the actual 

number of police beats required to carry 

out the experiment. 

Let us suppose that those secondary beats 

in a block sharing a side with the primary 

beat each contribute equally to the appropriate effect terms, while the four secondary beats that share only a corner with the 

primary beat contribute equal but lesser 

amounts (say 1/2 of the former). Then we 

can alter the number of beats in those 

blocks on a boundary, by eliminating as 

many secondary beats as necessary. For 

example, suppose we have a design with 

nine blocks laid out so that the experimental area takes the form of a 9 x 9 layout of 

square beats. If we have an actual area of 

roughly the same size but possessing 49 

beats in a 7 x 7 area, then we eliminate the 

secondary beats all around the original 

design resulting in the layout shown in 

Figure 3. 

Note that the 4 blocks in the corner have 

only 3 secondary beats, while 4 others have 

exactly 5, and only one block has 8. 

Analyzing designs laid out in a fashion 

similar to the one above requires modifications to the more or less standard analyses 

for the "complete" designs described earlier, but the modifications are straightforward, corresponding directly to the 

assumptions regarding the effects from the 

secondary beats described above. 

In Kansas City, not only can we reduce the 

number of beats required for our designs 

by taking advantage of the city boundaries, 

we can make similar reductions with blocks 

of beats bordering the Missouri River. The 

river slices across the city and, according to 

reports we have had, police patrolling beats 

on one side of the river rarely answer calls 

for service on the other side. Thus we may 

well be able to reduce the 108 beats 

required for implementing our 12-block 

balanced design to the 69 beats that 

actually exist in Kansas City. 

Some care must be taken in using the 

approach outlined here in order to ensure 

that all of the primary beats do not fall 

adjacent to city and natural boundaries. 

For example, if we have 4 blocks resulting 

in a 6 x 9 layout of beats, eliminating all of 

the exterior secondary beats leads to a layout with all 6 primary beats on the boundary. Some type of compromise would 

probably be wise in such circumstances. 

V. Further considerations 

and summary 

For policy decisions regarding police 

deployment and manpower allocation we 

require as precise estimates as possible of 

the effects of one policy versus another. 

Thus once we carry out all of the tests corresponding to the various sources in the 

ANOVA tables of the previous section, we 

should bolster our estimates of various 

effects by directly utilizing data from the 

secondary beats. Since reported crimes are 

already recorded by beat there would be no 

added cost for collecting additional data on 

the secondary beats. 

The experimental designs described in Section IV may easily be adapted for other 

experiments involving police deployment 

and manpower allocation, such as ones 

dealing with comparisons between the use 

of one-man and two-man patrol cars. 

We have noted earlier that the proposed 

experiment involves neither changes in 

police manpower nor the spatial redistribution of patrol resources within a city, as 

was the case in the KCPPE. Thus no policy 

implications regarding levels of manpower 

can possibly result. Moreover, since the 

different patrol strategies will be applied to 

small areas, even if the results are striking 

the policy implications for overall police 

patrol strategy in a city may be difficult to 

formulate due to the use of the different 

strategies in adjacent beats in the experiment. For example, if there is no detectable 

difference among treatment effects, we 

must ask if the results suggest a policy of 

"business as usual" or a new overall 

strategy of low visibility patrol. The answer 

seems unclear. 
Figure 3. 

Primary 

Secondary 

Finally we must ask how stable the 

estimates of parameters in the experimental model will be over time, and across 

cities. Variables that influence the behavior 

of offenders may interact with the experimental variables and with the peculiarities 

of cities and times in such a way as to make 

estimates highly unstable. If this is the case, 

then changes and refinements in the experimental design are required. Further consideration must be given to the potential 

policy implications of the experiment as 

part of the design. 

Many so-called social experiments are not 

really experiments in the formal statistical 

sense. All too often, when trying to evaluaTe whether some innovation or social program has the intended effect, investigators 

fail to provide a direct means for separating 

out or controlling for the effects of changes 

in concomitant variables. To overcome the 

difficulties inherent in such studies, social 

scientists have turned to the use of 

randomized controlled field trials. Both the 

randomization and the control are crucial 

to such studies. 

Many social experiments, as a result of 

their failure to control for various sources 

of variability, end up by proving the null 

hypothesis. The analysis of experimental 

results is structured toward rejecting the 

null hypothesis (typically that of no difference) in favor of some alternative, by giving 

heavy weight to the null hypothesis unless 

it is demonstrably false. The level of 

significance (the probability of falsely 

rejecting the null hypothesis) is set at some 

low value and then the probability of failing to detect the alternative hypothesis 

when it is true is made problematic. Unless 

that probability also is small, the experiment will be weighted in favor or the null 

hypothesis. Such, we have argued, was 

likely the case in the KCPPE because of its 

weak experimental design, i.e., its failure to 

control for important sources of variability. At least as crucial, in our view, was 

the failure of the KCPPE investigators to 

use proper randomization of treatments to 

experimental units. 

The problem of what design to adopt for 

social experiments is not easily resolved. 

Here we call attention to a particular class 

of designs that are useful not only for 

experiments relating to patrol strategies, 

but also to other types of social experiments. Our basic design has two key 

features: 

(1) Different treatments are applied to 

the same experimental units during different time periods, resulting in a crossover or 

changeover structure where each unit is Its 

own control. 

(2) Additional control is exercised through 

a specialdevice whereby primary experimental 

units are insulated from one another by the 

addition of secondary experimental units, 

with effects being examined in both the 

primary and secondary units. This paper 

explores different orders of complexity in 

this design and discusses means for 

evaluating tradeoffs among them. 

It is apparent that more complex experimental designs controlling for various 

sources of variation will in general be more 

costly, take longer periods of time, and 

involve greater use of repeated measures 

than the simple experimental design 

adopted for the KCPPE. If public policy is 

to rest On social experiments where causal 

inference is essential, the gain in efficiency 

associated with complex designs should 

ordinarily outweigh any increased cost. 

Appendix: 

Power calculationsfor comparing 

balanced and random designs 

for ANOVA models in Section IV 

The tables in this appendlx glve illustrations of 

the magnitude of effects capable of detection 

through the use of standard F-tests with an 0.05 

level of significance, with power = Pr(reject IH, 

true) = 0.50,0.70,0.90, and 0.95. Table A-l is for 

the 12-block experiment and the model with carryover effects. Table A-2 is for the 12-block 

experiment and residual effects. Table A-3 is for 

the 6-block experiment. At least two illustrations are given for each effect. 

For treatment and main effects, the tests were 

based on adjustments first for other maineffects 

(this is the standard form of analysis), and then 

for all other effects including interactions, carryover effects, and residual effects. 

How to read the tables. Suppose we are interested in compared experiments using an 0.05 

level of significance. Then the first set of rows in 

the table tell us that, if A = 4.550, B =O,and C= 

+0.550 (where 02 is the varlance of the random 

error term), the usual F-tests for treatments 

would have detected these effects for the balanced design with power = 0.50. 

Acknowledgments 

This paper grew out of mater~aldiscussed in the 

Workshop on Criminal Justice Statistics,held in 

Washington, D.C., July 1975,and sponsored by 

the Social Science Research Council Center for 

Coordination of Research on Social indicators 

and the Law Enforcement Assistance Administration. We are indebted to Davld W. Britt, 

William Falrly, Rlchard Larson, Katherine C. 

Lyall, and Richard Sparks for several important 

suggestions and comments. An abbreviated version of an earller draft of thls paper appeared 

under the same tltle in Evaluat~on3 (1976), 

124-131. 

During the preparation of this paper, Stephen E. 

Fienberg's research was partially supported by 

grants from The Robert Wood Johnson Foundation and the Commonwealth Fund to the 

Center for Analysis of Health Practices, 

Harvard School of Public Health, and from the 

National Science Foundation Grant SOC72-

05257 to the Department of Statistics, Harvard 

University. Albert J. Reiss' research was partially supported by a grant from the Russell Sage 

Foundation. 
Table A-1. Carry-over analysis 

50% Power 70% Power 90% Power 95% Power 

(a) Balanced Random Balanced Random Balanced Random Balanced Random 

Treatment effects A -.55 -.57 

(adjustingonly for B 0 0 

main effects) C +.55 +.57 

-.69 -.72 

0 0 

+.69 +.72 

-.89 -.93 

0 0 

+.89 +.93 

-.99 -1.03 

0 0 

+.99 +1.03 

Treatment effects A -.56 -.80 -.70 -1.02 -.91 -1.31 -1.01 -1.45 

(adjusting for an 8 0 0 

effects) C +.56 +.80 

0 0 

+.70 +1.02 

0 0 

+.91 +1.31 

0 0 

+1.01 +1.45 

Treatment effects A +.63 +.66 +.80 +.83 +1.03 +1.07 +1.14 +1.19 

(adjusting only for B -.32 -.33 

main effecw C -.32 -.33 

-.40 -.41 

-.40 -.4 1 

-.51 -.54 

-.51 -.54 

-.57 -.60 

-.57 -.60 

Treatment effects A +.67 +.98 +.85 +1.24 +1.09 +1.60 cl.21 +1.78 

(adjusting for &I B -.34 -.49 

effects) C -.34 -.49 

-.42 -.62 

-.42 -.62 

-.55 -.80 

-.55 -.80 

-.61 -.89 

-.61 -.89 

Insulation effects 01 -.55 -.57 -.69 -.72 -.89 -.93 -.99 -1.03 

(adjusting only for 0 0 

main effects) Y +.55 c.57 

0 0 

+.69 +.72 

0 0 

+.89 +.93 

0 0 

+.99 +1.03 

Insulation effects ff -.56 -.96 -. 70 -1.20 -.91 -1.55 -1 .O1 -1.73 

(adjusting for all P 0 0 

effects) Y c.56 +.96 

0 0 

+.70 -1.20 

0 0 

+.91 +1.55 

0 0 

+1.01 +1.73 

Insulation effects a +.63 +.64 

(adjusting only for P -.32 -.32 

main effects) Y -.32 -.32 

+.80 +.81 

7.40 -.40 

-.40 -.40 

+1.03 +1.04 

-.51 -. 52 

-.51 -.52 

+1.14 +1.16 

-.57 -. 58 

-.57 -. 58 

Insulation effects a c.63 +.99 +.80 +1.25 +1.03 +1.61 +1.14 +1.79 

(adjusting for &I 0 -.32 -. 50 

effects) Y -.32 -. 50 

-.40 -.62 

-.40 -.62 

-.51 -.81 

-.51 -.81 

-.57 -.90 

-.57 -.90 

(b) Treatment A before C +l. 18 +1.84 +1.47 +2.30 +1.89 +2.95 +2.08 +3.24 

carry-over B before C --1.18 -1.84 

effects A before B +.59 +.92 

-1.47 -2.30 

+.74 +1.15 

-1.89 -2.95 

+.95 +1.48 

-2.08 -3.24 

+1.04 +1.62 

C before B -. 59 -.92 -. 74 -1.15 -.95 -1.48 -1.04 -1.62 

B before A 0 0 0 0 0 0 0 0 

C before A 0 0 0 0 0 0 0 0 

Treatment A before C 0 0 0 0 0 0 0 0 

carry-over B before C 0 0 

effects A before B 0 0 

0 0 

0 0 

0 0 

0 0 

0 0 

0 0 

C before B 0 0 0 0 0 0 0 0 

B before A +1.53 +1.53 

C before A -1.53 -1.53 

+1.91 +1.91 

-1.91 -1.91 

+2.45 +2.46 

-2.45 -2.46 

+2.69

- +2.70 

- Insulation ff before y +1.18 +1.38 

carry-over p before y -1.18 -1.38 

effects a before +.59 +.69 

y before P -. 59 -.69 

before a 0 0 

+1.48 +1.73 

-1.48 -1.73 

+.74 +.86 

-. 74 -.86 

0 0 

+1.90 +2.20 

-1.90 -2.20 

+.95 +1.10 

-.95 -1.10 

0 0 

+2.07 +2.44 

-2.07 -2.44 

+1.04 +1.22 

-1.04 -1.22 

0 0 

y before a 0 0 0 0 0 0 0 0 

Insulation a before 7 0 0 0 0 0 0 0 0 

carry-over 0 before y 0 0 

effects a before /3 0 0 

y before 0 0 0 0 before a +1.52 +1.84 

0 0 

0 0 

0 0 

+1.90 +2.30 

0 0 

0 0 

0 0 

+2.44 +2.96 

0 0 

0 0 

0 0 

+2.68 +3.25 

y before a -1.52 -1.84 -1.90 -2.30 -2.44 -2.96 -2.68 -3.25 

(c) Interaction Aff +5.16 +3.72 +6.37 +4.59 +8.19 +5.91 +8.95 +6.45 

effects AP -.65 -.47 -.80 -.57 -1.02 -. 74 -1.12 -.81 

-.65 -.47 -.80 -.57 -1.02 -. 74 -1.12 -.81 

-.65 -.47 -.80 -.57 -1.02 -. 74 -1.1 2 -.81 

BP -.65 -.47 -30 -.57 -1.02 -.74 -1.12 -.81 

By -.65 -.47 

Car -.65 -.47 

-.80 -.57 

-.80 -.57 

-1.02 -.74 

-1.02 -.74 

-1.12 -.81 

-1.12 -.81 

CP -.65 -.47 -.80 -. 57 -1.02 -.74 -1.12 -.81 

C7 -.65 -.47 -.80 -.57 -1.02 -.74 -1.1 2 -.81 

Interaction Aa +3.39 +1.90 +4.18 +2.34 +5.38 +3.01 +5.87 +3.29 

effects Ap -.97 -. 54 -1.19 -.67 -1.54 -.86 -1.68 -.94 

A7 -.97 -.54 -1.19 -.67 -1.54 -.86 -1.68 -.94 

801 -.97 -.54 -1.19 -.67 -1.54 -.86 -1.68 -.94 

BP +1.94 +1.08 +2.39 +1.34 +3.07 +1.72 +3.36 +1.88 

87 -.97 -. 54 -1.19 -.67 -1.54 -.86 -1.68 -.94 

Car -.97 -.54 -1.19 -.67 -1.54 -.86 -1.68 -.94 

CP -.97 -. 54 -1.19 -.67 -1.54 -.86 -1.68 -.94 

Cy +.48 +.27 +.60 +.33 +.77 +.43 +.84 +.47 

Interaction Act +2.00 +1.12 +2.47 +1.38 +3.17 +1.78 +3.47 +1.94 

effects Ap -1.00 -.56 

-1 .OO -. 56 

-1.23 -.69 

-1.23 -.69 

-1.59 -.89 

-1.59 -.89 

-1.73 -.97 

-1.73 -.97 

-1.00 -.56 -1.23 -.69 -1.59 -.89 -1.73 -.97 

B@ +2.00 +1.12 +2.47 +1.38 +3.17 +1.78 +3.47 +1.94 

By -1.00 -. 56 

Ccl -1.00 -.56 

--1 .OO -. 56 :; +2.00 +1.12 

-1.23 -.69 

-1.23 -.69 

-1.23 -.69 

+2.47 +1.38 

-1.59 -.89 

-1.59 -.89 

-1.59 -39 

+3.17 +1.78 

-1.73 -.97 

-1.73 -.97 

-1.73 -.97 

+3.47 +1.94 
Table A-2. Residual analysis 

50% Power 70% Power 90% Power 95% Power 

(a) Balanced Random Balanced Random Balanced Random Balanced Random 

Treatments (adjusting -.53 -.55 -.66 -.68 -.85 -.89 -.94 -.98 

only for main effects) 0 0 0 0 0 0 0 0 

+.53 +.55 +.66 +.68 +.85 +.89 +.94 +.98 

Treatments (adjusting -.62 -.81 -.77 -1 .OO -.99 -.85 -1.10 -1.44 

for alleffects1 0 0 0 0 0 0 0 0 

+.62 +.81 +.77 +1 .OO +.99 +.85 +1.10 +1.44 

Treatments (adjusting +.61 +.64 +.76 +.79 +.98 +1.03 +I .09 +1.14 

only for main effects) -.31 -.32 -.38 -.40 -.49 7.51 -.55 -.57 

-.3 1 -.32 -.38 -.40 -.49 -.51 -.55 -.57 

Treatments (adjusting 

for eeffects) 

+.71 

-.35 

+I .09 

-. 54 

+.88 

-.44 

+1.35 

-.68 

+1.14 

-.57 

+1.75 

-.8 7 

+I .26 

-.63 

+I .94 

-.97 

-.35 -.54 -.44 -.68 -.57 -.87 -.63 -.97 

Insulation (adjusting -.53 -.55 -.66 -.69 -.85 -.89 -.94 -.99 

only for main effects) 0 

+.53 

0 

+.55 

0 

+.66 

0 

+.69 

0 

+.85 

0 

+.89 

0 

+.94 

0 

+.99 

Insulation (adjusting -.62 -.9 1 -.77 -1.13 -.99 -1.46 -1.10 -1.62 

for glJ effects) 0 0 0 0 0 0 0 0 

+.62 +.91 +.77 +1.13 +.99 +I .46 +1.10 +1.62 

Insulation (adjusting . +.61 +.62 +.76 +.77 +.98 +.99 +1.09 +1.10 

only for main effects) -.31 -.31 -.38 -.38 -.49 -.50 -.55 -.55 

-.31 -.31 -.38 -.38 -.49 -.50 -.55 -.55 

Insulation (adjusting +.72 +.89 +.89 +1.11 +1.15 +1.44 +1.28 +I .59 

for glJ effects) -.36 

b.36 

-.45 

-.45 

-.44 

-.44 

-.55 

-.55 

-.58 

-.58 

-.72 

-.72 

-.64 

-.64 

-.go 

-.SO 

(b) 

Treatment After A -.89 -1.24 -1.10 -1.54 -1.42 -2.00 -1.58 -2.21 

residual After B 0 0 0 0 0 0 0 0 

After C +.89 +1.24 +1.10 +1.54 +1.42 +2.00 +1.58 +2.21 

Treatment After A 

residual After B 

+1.07 

-. 54 

+1.49 

-.75 

+1.33 

-.67 

+1.85 

-.93 

+I .72 

-.86 

+2.40 

-1.20 

+1.91 

-.96 

+2.66 

-1.33 

After C -.54 -.75 -.67 -.93 -.86 -1.20 -.96 -1.33 

Insulation After ff 

residual After P -.89 

0 

-1.11 

0 

-1.10 

0 

-1.38 

0 

-1.42 

0 

-1.79 

0 

-1.58 

0 

-1.98 

0 

After y +.89 +1.11 +1.10 +1.38 +1.42 +1.79 +I .58 +I .98 

Insulation After ff 

residual After P 

After y 

+I .OO 

-.50 

-.50 

+1.25 

-.62 

-.62 

+1.24 

-.62 

-.62 

+1.54 

-.77 

-.77 

+I .61 

-.SO 

-.80 

+2.00 

-1 .OO 

-1 .OO 

+1.78 

-.89 

-.89 

+2.22 

-1.11 

-1.11 

Interaction Aff +3.11 +3.45 +3.83 +4.24 +4.88 +5.40 +5.33 +5.91 

A@ -.39 -.43 -.48 -.53 -.61 -.68 -.67 -.74 

A7 -.39 -.43 -.48 -.53 -.61 -.68 -.67 -.74 

Bff 

SP 

BY 

Cff 

CP 

CY 

-.39 

-.39 

-.39 

-.39 

-.39 

-.39 

-.43 

-.43 

-.43 

-.43 

-.43 

-.43 

-.48 

-.48 

-.48 

-.48 

p.48 

-.48 

-.53 

-.53 

-. 53 

-. 53 

-.53 

-.53 

-.61 

-.61 

-.61 

-.61 

-.61 

-.61 

-.68 

-.68 

-.68 

-.68 

-.68 

-.68 

-.67 

-.67 

-.67 

-.67 

-.67 

-.67 

-.74 

-. 74 

-. 74 

-.74 

-.74 

-. 74 

(c) 

Interaction Ao! 

effects AP 

2 

+I .90 

-.54 

-. 54 

-.54 

+1.74 

-. 50 

-.50 

-.50 

+2.35 

-.67 

-.67 

-.67 

+2.15 

-.61 

-.61 

-.61 

+2.98 

-.85 

-.85 

-.85 

+2.73 

-. 78 

-.78 

-. 78 

+3.26 

-.93 

-.93 

-.93 

+2.99 

-.85 

-.85 

7.85 

BP 

BY 

Cff 

+1.09 

-.54 

-.54 

+1 .OO 

-. 50 

-. 50 

+1.34 

-.67 

-.67 

+I .23 

-.61 

-.61 

+1.71 

-.85 

-.85 

+1.56 

-.78 

-.78 

+1.87 

-.93 

-.93 

+1.71 

-.85 

-.85 

CP -. 54 -.50 -.67 -.61 -.85 -.78 -.93 -.85 

CY +.27 +.25 +.34 +.31 +.43 +.39 +.47 +.43 

Interaction Aff 

effects AP 

+1.14 

-.57 

+I .03 

-.52 

+I .40 

-.70 

+1.27 

-.64 

+1.78 

-. 89 

+I .62 

-.81 

+1.95 

-.98 +I .77 -.89 

AY 

BCY 

-.57 

47 

-.52 

-. 52 

-.70 

-.70 

-.64 

-.64 

-.89 

-.89 

-.81 

-.81 

-.98 

-.98 

-.89 

-.89 

BP +1.14 +1.03 +I .40 +1.27 +1.78 +1.62 +1.95 +1.77 

67 -.57 -.52 -.70 -.64 -.89 -.81 -.98 -.89 

Cff c@ -.57 

-.57 

-.52 

-.52 

-.70 

-.70 

-.64 

-.64 

-.89 

-.89 

-.81 

-.81 

-.98 

-.98 

-.89 

-. 89 

CY +1.14 +1.03 +1.40 +I .27 +1.78 +I .62 +1.95 +1.77 

I 
I ( Table A-3. 6-beat analysis 

50% Power .70% Power 90% Power 95% Power 

Balanced Random Balanced Random Balanced Random Balanced RandomI 

Treatment 


effects 


Treatment 


effects 


Insulation 


effects 


Insulation 


effects 


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Nationai Criminai Justice Reference Service, Box 

6000, Rockviiie, Md. 20850. Multiple copies are for 

sale by the Superintendent of Documents, U.S. 

Government Printing Office, Washington, D.C. 

20402. 

National Crime Survey: 

Criminal Victimization in the United States 

(annual): 

Summary Findings of 1977-78 Changes in 


Crime and of Trends Since 1973, NCJ- 


61 368 


A Description of Trends from 1973 to 1977. 

NCJ-59898 


1978 (final report), NCJ-66480 


1977, NCJ-58725 


1976, NCJ-49543 


1975, NCJ-44593 


1974, NCJ-39467 


1973. NCJ-34732 


The Cost of Negligence: Losses from 


Preventable Household Burglaries, 


NCJ-53527 


Intimate Victims: A Study of Violence Among 

Friends and Relatives, NCJ-62319 


Crime and Seasonality, NCJ-64818 


Criminai Victimization of New York State 


Residents, 1974-77, NCJ-66481 


Criminai Victimization Surveys in 13 


American cities (summary report. 1 vol.), 


NCJ-18471 


Boston, NCJ-34818 


Buffalo, NCJ-34820 


Cincinnati, NCJ-34819 


Houston, NCJ-34821 


t:c: Miami, NCJ-34822 


- Milwaukee, NCJ-34823 


. Minneapolis, NCJ-34824 


T< New Orleans, NCJ-34825 
 %_-- Oakland, NCJ-34826 


Pittsburgh, NCJ-34827 
 a-
>> San Diego, NCJ-34828 


San Francisco, NCJ-34829 


Bg' Washington, D.C., NCJ-34830 


Public Attitudes About Crime (13 vols.): 
 0 Boston, NCJ-46235 


Buffalo, NCJ-46236 


{- @ Cincinnati, NCJ-46237 


Houston, NCJ-46238 


c? Miami, NCJ-46239 
 k$J! Failwaukee, NCJ-46240 
 8 
,:Minneapolis, NCJ-46241


<New ~rieans, NCJ-46242 


c_%akiand, NCJ-46243 


;j.:Fttsburgh, NCJ-46244 


- :-%an Diego, NCJ-46245 


c5 : '::Sari Francisco, NCJ-46246 
 -- ..-,Washington, D.C., NCJ-46247 


,:k !Q'iminai Vlctlmization Surveys in Chicago, 
 2.- -rtlDetroit, Los Angeles, New York, and 2 (3 :,;Philadelphia: A Comparison of 1972and G, ---. rl" ,-,,:.:-I974 Findings. NCJ-36360 


.-- (:*,I Griminai Victimization Surveys in the 


+a 
 -. . 7: jNation's Five Largest Cities: National 

,.*-':'3 ?? :.:'Crime Panel Surveys in Chicago, Detroit. ,P pi., I !" re-- --, 	Los Angeles. New York, and Philadelphia, 


1972, NCJ-16909 


Criminai Victimization Surveys in Eight 


American Cities: A Comparison of 1971/72 


and 1974/75 Findings-National Crime 


Surveys in Atlanta, Baltimore, Cleveland, 


Dallas. Denver, Newark, Portland, and St. 


Louis, NCJ-36361 


Crimesand Victims: A Report on the Dayton/ 


San Jose Pilot Survey of Victimization, 


NCJ-013314 


Indicators of Crime and Criminai Justice: 


Quantitative Studies, NCJ-62349 


Applications of the National Crime 

Survey Victimization and Attitude Data: 

Pubiic Opinion About Crime: The Attitudes 


of Victims and Nonvictims in Sglected 


Cities. NCJ-41336 


Locai Victim Surveys: A Review of the 


issues, NCJ-39973 


The Police and Pubiic Opinion: An Analysis 


of Victimization and Attitude Data from 


13 Amerlcan Cities. NCJ-42018 


An Introduction to the Nationai Crime 


Survey, NCJ-43732 


Compensating Victims of Vioient Crime: 


Potential Costs and Coverage of a National 


Program, NCJ-43387 


Crime Against Persons in Urban, Suburban, 


and Rural Areas: A Comparative Analysis of 


Victimlzation Rates. NCJ-53551 


IIap; ~ictimizationin 26 American Cities, 


NCJ-55878 


Criminai Victimization in Urban Schools, 


NCJ-56396 


National Prisoner Statistics: 


Capital Punishment (annual): 


1978, NCJ-59897 


1979advance report, NCJ- 67705 


Prisoners in State and Federai Institutions on 


December 31: 


1978, NCJ-64671 


1979 advance report, NCJ-66522 


Census of State Correctional Facilities, 1974 


advance report, NCJ-25642 


Profile of State Prison Inmates: Socio- 


demographic Findingsfrom the 1974 Survey 


of Inmates of State Correctional Facilities, 


NCJ-58257 


Census of Prisoners in State Correctional 


Facilities, 1973, NCJ-34729 


Census of Jaiis and Survey of Jail inmates, 


1978, preliminary report. NCJ-55172 


Rofile of Inmates of Local Jaiis: Socio- 


demographic Findingsfrom the 1978 Survey 


of inmates of Locai Jaiis, NCJ-65412 


The Nation's Jaiis: A report on the census 


of jails from the 1972 Survey of inmates of 


Local Jails, NCJ-19067 


Survey of Inmates of Local Jails, 1972, 


advance report. NCJ-13313 


Uniform Parole Reports: 

Parole in the United States (annual): 


1978, NCJ-58722 


1976 and 1977, NCJ-49702 


Characteristics of the Parole 


Population, 1978, NCJ-66479 


A National Survey of Parole-Related 


Legislation Enacted During the 1979 


Legislative Session. NCJ-64218 


Children in Custody: Juvenile Detention and 

Correct.ional Facility Census 

1977 advance report: 

Census of Public Juvenile Facilities. 


NCJ-60967 


Census of Private Juvenile Faciiities, 


NCJ-60968 


1975 (final report). NCJ-58139 


1974, NCJ-57946 


1973, NCJ-44777 


1971, NCJ-I3403 


Myths and Realities About Crime: A 


Nontechnical Presentation of Selected 


information from the Nationai Prisoner 


Statistics Program and the National Crime 


Survey, NCJ-46249 


State and Locai Probation and Parole Systems, 


NCJ-41335 


State and Locai Prosecution and Civil Attorney 


Systems, NCJ-41334 


National Survey of Court Organization: 


1977 Supplement to State Judicial Systems, 


NCJ-40022 


1975 Supplement to State Judicial Systems. 


NCJ-29433 


1971 (full report). NCJ-11427 


State Court Model Statistical Dictionary, 


NCJ-62320 


State Court Caseload Statistics: 


The State of the Art. NCJ-46934 


Annuai Report, 1975. NCJ-51885 


Annuai Report, 1976. NCJ-56599 


A Cross-City Comparison of Felony Case 


Processing, NCJ-55171 


Trends in Expenditure and Employment Data 


for the Criminal Justice System, 1971-77 


(annual), NCJ-57463 


Expenditure and Employment Data for the 


Criminai Justice System (annual) 


1978Summary Report, NCJ-66483 


1978 final report. NCJ-66482 


1977 final report, NCJ-53206 


Dictionary of Criminai Justice Data Terminology: 


Terms and Definitions Proposed for interstate 


and National Data Collection and Exchange, 


NCJ-36747 


Justice Agencies in the U.S.: 


Summary Report of the National 


Justice Agency List, NCJ-65560 


Criminal Justice Agencies in Region 

1: Conn., Maine, Mass., N.H., R.I., Vt., 


NCJ-17930 


2: N.J.. N.Y., NCJ-17931 


3: Del., D.C., Md., Pa., Va., W.Va., NCJ-17932 


4: Aia.. Ga., Fla.. Ky.. Miss.. N.C., S.C., Tenn., 

NCJ-I7933 

5: 	 Iii., Ind., Mich., Minn., Ohio, Wis., NCJ- 


17934 


6: Ark., La., N.Mex., Okla., Tex., NCJ-17935 


7: Iowa. Kans.. Mo., Nebr., NCJ-17936 


8: Colo., Mont.. N.Dak.. S.Dak., Utah. Wyo.. 

NCJ-I7937 

9: Ariz., Calif., Hawaii, Nev., NCJ-15151 


10: Alaska, Idaho, Oreg., Wash., NCJ-17938 


Utilization of Criminal Justice Statistics 


Project: 


Sourcebook of Criminal Justice Statistics 


1979 (annual), NCJ-59679 


Pubiic Opinion Regarding Crime, Criminal 


Justice, and Related Topics, NCJ-17419 


New Directions in Processing of Juvenile 


Offenders: The Denver Model, NCJ-! 7420 


Who Gets Detained?An Empirical Analysis 


of the Pre-Adjudicatory Detention of 


Juveniles in Denver. NCJ-17417 


Juvenile Dispositions: Social and Legal 


Factors Related to the Processing of Denver 


Deiinquency Cases, NCJ-17418 


Offender-Based Transaction Statistics: New 

Directions in Data Collection and Reporting, 

NCJ-29645 . -.-..-

Sentencing of California Felony Offenders, 


NCJ-29646 


The Judicial Processing of Assault and 


Burglary Offenders in Selected California 


Counties, NCJ-29644 


Re-Adjudicatory Detention in Three Juvenile 


Courts, NCJ-34730 


Deiinquency Dispositions: An Empirical 


Analysis of Processing Decisions in Three 


Juvenile Courts, NCJ-34734 


The Patterns and Distribution of Assault 


Incident Characteristics Among Social 


Areas. NCJ-40025 


Patterns of Robbery Characteristics and Their 


Occurrence Among Social Areas. NCJ-40026 


Crime-Specific Anaiysis: 


The Characteristics of Burglary incidents. 


NCJ-42093 


An Empirical Examination of Burglary 


Offender Characteristics. NCJ-43131 


An Empirical Examination of Burglary 


Offenders and Offense Characteristics, 


NCJ-42476 


Sources of Nationai Criminai Justice 


Statist!cs:An Annotated Bibliography. 


NCJ-45006 


Federal Criminal Sentencing: Perspectives 


of Analysis and a Design for Research, 


NCJ-33683 


Variations in Federal Criminai Sentences: 


A Statistical Assessment at the National 


Level, NCJ-33684 


Federai Sentencing Patterns: A Study of 


Geographical Variations. NCJ-33685 


Predicting Sentences in Federal Courts: The 


~easibiiity of a National Sentencing Policy, 


NCJ-33686