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Document Title: Does Batterer Treatment Reduce Violence? A

Randomized Experiment in Brooklyn –

Executive Summary Included

Author(s): Robert C. Davis ; Bruce G. Taylor ; Christopher

D. Maxwell

Document No.: 180772

Date Received: February 8, 2000

Award Number: 94-IJ-CX-0047

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I go 

Does Batterer Treatment Reduce Violence? 

A Randomized Experiment in Brooklyn 

Robert C. Davis 

Bruce G. Taylor 

Christopher D. Maxwell 

Victim Services Research 

346 Broadway, Suite 206 

NY, NY 10013 

January 3, 2000 

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ABSTRACT 

During the past two decades, pro-arrest laws have resulted in 

an increasing number of prosecutions of men who assault spouses or 

girlfriends. Researchers and practitioners have documented the 

difficulty of altering the behavior of convicted spouse abusers. As 

the courts have searched for effective sanctions for spouse abusers, 

they have increasingly come to rely on group treatment programs as 

the sentence of choice for the widening pool of men convicted of 

spousal assault. 

The greater reliance on batterer treatment programs makes it 

important that we can document that such programs effectively reduce 

the propensity of offenders to commit new violence. There is no 

shortage of evaluations of batterer treatment programs: Some three 

dozen have appeared in the literature since the 1980s. Most of 

these studies have methodological deficiencies, which make it 

difficult to interpret their findings. But evaluation studies have 

become more sophisticated as time has passed. 

The present study represents one of the first attempts to 

conduct a test of batterer treatment using a true experimental 

design. The design randomly assigned 376 court-mandated batterers 

to batterer treatment or to a treatment irrelevant to the battering 

problem (community service). All men assigned to batterer treatment 

were mandated to 39 hours of class time. But some were assigned to 

complete the treatment in 26 weeks and others in eight weeks. Men 

assigned to the control condition were sentenced to forty hours of 

community service. For all cases in the study, interviews were 

attempted with victims and batterers at 6 months and 12 months after 

the sentence date. In addition, records of criminal justice 

agencies were checked to determine if new crime reports or arrests 

had occurred involving the same defendant and victim. 

The results showed that treatment completion rates were higher 

for the eight-week group than for the 26-week group. However, only 

defendants assigned to the 26-week group showed significantly lower 

recidivism at 6 and 12 months post-sentencing compared to defendants 

assigned to the control condition. The groups did not differ 

significantly at either 6 or 12 months in terms of new incidents 

reported by victims to research interviewers. We interpret the 

results to indicate that batterer intervention has a significant 

effect on suppressing violent behavior while batterers are under 

court control, but may not produce 

e 

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INTRODUCTION 

Over the past two decades, the law enforcement response to 

domestic violence has become increasingly tough. Pro-arrest police 

policies have been promoted by advocates and widely adopted by 

police departments across the country (Buzawa and Buzawa, 1996). 

Increasingly, prosecutors as well have removed discretion 

traditionally given victims of domestic,violence and insisted that 

cases be pursued to conviction regardless of victim desires or 

willingness to cooperate (Rebovich, 1996; Hanna, 1996). These 

changes have meant that criminal courts have had to sanction an 

expanding pool of batterers, and they have increasingly come to 

rely upon group treatment programs as the sanction of choice. 

There are compelling reasons why group treatment programs for 

batterers have become Even in 

serious battering cases, many victims choose to stay with abusive 

partners. Such victims are interested in sanctions which offer 

them safety from violence, not retribution or punishment that will 

jeopardize their partner’s ability to earn a living. Alternative 

sanctions commonly used in other crimes have little face validity 

in abuse cases: There is little reason to believe that fines, 

community service or probation without special conditions will stop 

batterers from abusing their spouses. 

3 

a popular mode of court sanction. 

There is no shortage of evaluations of batterer treatment 

programs. But the vast majority has serious methodological flaws 

which make it impossible to distinguish between treatment effects, 

0 temporal effects, and selection effects. Generally, the evaluation 

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literature shows an evolution toward more rigorous science since 

the first batterer treatment studies appeared in the literature in 

the early 1980s. The study we describe represents one of the first 

attempts to conduct a test of batterer treatment using a true 

experimental design which randomly assigns court-mandated batterers 

to batterer treatment or to a control condition. 

The Nature of Batterer Treatment 3 

The first group programs for batterers were begun during the 

late 1970s. Feminists, victim advocates, and others realized that 

providing services to victims of abuse and then returning them to 

the same home environment did little to solve abuse problems 

(Healey, Smith, and O'Sullivan, 1997). Group treatment was 

believed to be more appropriate than individual counseling or 

marital therapy because it expanded the social networks of 

batterers to include peers who are supportive of being nonabusive 

(Crowell and Burgess, 1996). Groups also proved to be less 

expensive than one-on-one counseling sessions. The earliest 

batterer groups were educational groups which sought to promote an 

anti-sexist message (Gondolf, 1995). With the passage of time, 

they gradually incorporated cognitive/behavioral therapeutic 

techniques and skill-building exercises. 

As states introduced pro-arrest statutes during the 1980s the 

number of batterers arrested and convicted increased, and group 

treatment became the treatment of choice for the courts. Courtmandated batterer treatment significantly increased and diversified 

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the number of batterer programs nationally (Feazell, Mayers, & 

Deschner, 1984). A recent estimate places the proportion of court 

mandates in treatment programs at 80% (Healey, et. al. 1997). 

0 

Batterer treatment may be required by criminal courts as part 

of a pre-trial diversion program, may be ordered by judges as part 

of a sentence, or may be imposed by probation agencies empowered to 

set special conditions of probation (Hamberger & Hastings, 1993). 

In at least one major urban jurisdiction, the district attorney -. 

sometimes agrees not to file charges at all if a brief treatment 

program is completed (Davis and Smith, 1997). In some states (see 

Ganley, 19871, civil courts as well as criminal may mandate a 

batterer to treatment (e.g., as a condition related to child 

visitation). 

Many batterer programs are run by probation departments, while 

others are run by mental health practitioners, family service 

organizations, or victim service programs. Intake practices vary, 

with some programs accepting all court referrals and others 

exercising discretion in excluding persons with prior convictions 

or substance abuse problems. Supervision of batterers in treatment 

can most often falls to probation officers, but is sometimes 

undertaken by others - and increasingly by judges. Historically, 

supervision has been lax, drop out rates high, and sanctions 

unevenly applied. Recently, however , supervision has become 

stricter and sanctions for failure to attend sessions more common. 

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Program Typologies 

Different perspectives on wife battering place the cause 

within individuals (personality or psychological abnormalities of 

batterers), within family dynamics (dysfunctional communication), 

or within the community (societal attitudes supporting violence). 

There are a wide variety of batterer treatment programs which 

address several of these three different levels of causation. 

Adams (1988) and Hamberger and Hastings (1993) differentiate 

batterer treatment groups according to five philosophical 

3 

orientations. The feminist framework is a political approach which 

proposes that male-to-female violence is rooted in a patriarchal 

society which provides power to men and oppresses women (Hamberger 

and Hastings, 1993). Domestic violence is seen as a means of 

establishing and maintaining male dominance, and is viewed as a byproduct of male and female sex roles. Subordinate economic roles 

have made women dependent on men and unable to leave their abusive 

situation. Feminist-based treatment programs rely primarily on 

"re-educating" batterers about the roles of men and women and about 

appropriate behavior in intimate relationships. 

The cognitive-behavioral model, based on social learning 

theory, views domestic violence as behavior learned by batterers 

through direct observation of role models, indirect observation 

(e.g., through the media), and direct 'trial and error" learning 

experiences (Hamberger and Hastings, 1993: 199). Violence is seen 

as functional for the perpetrator (e.g., tension release, avoidance 

of unpleasant tasks, and enforced victim compliance). Batterer 

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groups based on this model teach batterers conflict avoidance 

a techniques, assertiveness skills, relaxation skills, and cognitive 

strategies for reevaluating and neutralizing anger-producing 

thoughts. 

The ventilation model views partner violence as symptomatic of 

suppressed anger that needs to be expressed through some other 

means This model is rooted in family dynamics and views both 

partners as responsible for the violence. Batterers, and often 

their partners as well are assigned to groups which w6rk on 

developing better communication within the dyadic relationship. 

The insight-oriented model views domestic violence as a 

symptom of underlying problems from the batterer's past (e.g., 

residual fear or anger from past abuse from parents) that 

unconsciously motivates current violent behavior (Hamberger and 

0 Hastings, 1993: 197) . Treatment involves examining inner-life 

experiences, past experiences, and current interactions with 

others. 

The systems model is based on the idea that domestic violence 

is spawned by competition for control in dyadic relationships in 

which each partner attempts to dominate and control the other 

(Hamberger and Hastings, 1993). The early stages of this process 

begin with verbal and emotional abuse, but as both partners strive 

to win, one of the partners may resort to violence. Both parties 

participate in groups together. The group works on helping each 

partner identify their role in the violence, and improving 

communication skills (Adams, 1988). 

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In practice, modern batterer groups tend to mix different 

theoretical approaches to treatment (Healey, et. al. 1997), 

although most batterer programs are based upon the feminist model 

developed by the Domestic Abuse Intervention Project in Duluth, 

Minnesota. The Duluth model assumes that physical violence is 

part of a spectrum of male efforts to control women. But batterer 

programs also commonly deal with the need for anger control, stress 

management, and better communication skills. s 

Not only treatment approach, but treatment length varies from 

program to program. The duration or number of sessions may vary 

from as little as one day to 32 weeks (Feaze1 et al., 1984). Some 

in the field even have advocated long-term treatment from 1 to 5 

years (Ewing, Lindsey, & Pomerantz, 1984). However, there also is 

substantial pressure to keep batterer treatment short in duration 

resulting from pressure from insurance companies' imposition of 

time limits for batterers seeking reimbursement (Edelson and Syers, 

1990). 

Current trends in treatment programs seem to be going in 

conflicting directions. Increasingly, states are developing 

guidelines to codify standards for treatment content and length 

among batterer treatment programs (Gondolf, 1995). But, on the 

other hand, there is increasing sentiment that a "one-size fits 

all" approach to batterer treatment fails to recognize the 

diversity of batterers that enter treatment (Healey, et. al. 1997). 

There is a trend for treatment programs to tailor interventions to 

different batterer types defined by personality, violence history, 0 

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or substance abuse. Other programs have been specially designed to 

accommodate sociocultural differences among batterers such as 

poverty, ethnicity, or sexual orientation. 

a 

The Evaluation Literature 

Over the last two decades there have been many empirical 

studies on batterer treatment programs. There are at least six 

published reviews of over 35 published single-site evalugtions 

(e.g., Eisikovits & Edlespn, 1989; Gondolf, 1991,1995; Rosenfield, 

1992; Saunders, 1996a; Tolman & Bennett, 1990) and eight research 

reviews (e.g. , Davis and Taylor, in press; Hamberger & Hastings, 

1993; Crowell & Burgess, 1996; Dobash, Dobash, Cavanagh & Lewis, 

1995; Dutton, 1988, 1995; Rosenbaum & O'Leary, 1986; Saunders & 

Azar, 1989; Tolman & Edleson, 1995). Since these literature 

reviews a number of new studies have been conducted and published. 

However, the volume of the literature is deceptive. In fact, 

there have been only a handful of investigations that can make any 

legitimate claims about differences between treated batterers and 

untreated batterers. The batterer treatment literature has gone 

through three generations of studies. Most recent have been 

investigations which have randomly assigned batterers to treatment 

conditions. These are the strongest designs. Quasi-experiments of 

varying quality appeared somewhat earlier in the literature. The 

oldest, and by far the largest, portion of the empirical literature 

consists of studies which examine only batterers assigned to 

treatment programs. Included in this set of studies are: (a) 

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studies which assess violence or other individual outcomes only 

after batterer treatment, (b) studies which measure violence before 

and after treatment, and 0 studies which compare violence of 

batterers who complete treatment with batterers assigned to 

treatment, but do not attend. Although the methodologies of early 

studies do not tend to be strong, they are important because they 

laid the foundation upon which stronger designs could be developed. 

3 Methodological Issues in the Literature 

In order to intelligently evaluate treatment outcome studies, 

it is important to have in mind some of the methodological 

shortcomings common in this literature. This section outlines 

some of In 

the reviews which follow this section, we will draw upon this 

understanding to evaluate particular investigations and groups of 

studies. 

the major problems which are common to many studies. 

First, there has been a lack of consensus on how to measure 

program effects. Studies have measured program effects on violence 

using official data on arrests and complaints, victim surveys, and 

batterer surveys. Rosenfeld's (1992) review makes the point in 

detail that official reports of violence and batterer surveys 

seriously underestimate actual violence committed in relationships. 

Moreover, some studies (e.g. Mauiro, Cahn, Vitaliano, and Zegree 

1987) have not included any indicators of violence in their outcome 

measures. (Such studies are not included in our review.) Follow-up 

intervals have varied greatly, from several months to several 

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years. 

Studies differ widely in their statistical sophistication. 

0 

While most have reported inferential statistics examining 

differences between means, a few have merely presented percentage 

differences. Some studies which did use inferential statistics 

were conducted without sufficient statistical power to detect 

differences between treated and untreated participants. Some of 

the best quasi-experiments have incorporated multivariate analyses 

which attempt to control for the effects of extraneous variables 

when isolating treatment effects. 

Studies have varied in terms of the populations they are 

investigating. Obviously, the samples in these studies are not 

going to representative of all batterers in the United States, or 

even all batterers mandated to batterer treatment in the United 

States. Most researchers would probably be satisfied with 

demonstrating that batterer programs are effective for some welldefined group of batterers in one court system, in one city. 

Clearly, obvious sample selection biases should be avoided. 

One such sample selection bias is that most of the batterer 

programs that have been evaluated exclude difficult batterers 

(e.g., recidivist batterers or those who have substance abuse 

problems) from their programs. Elimination of potentially 

difficult subjects may overestimate the successfulness of treatment 

programs, were these programs forced to accept these more difficult 

cases (Rosenfeld, 1992). Therefore, the results of many of these 

studies may apply only to a limited spectrum of batterers. 

0 

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The problem of generalizeability of results also crops up in 

another way. Many treatment studies which have relied on batterer 

or victim surveys to assess violence have had poor interview 

response rates, some as low as 30%. Low response rates are a 

problem because the cases in which follow-up data are available may 

be different than those cases which data are not available. For 

example, Edleson and Syers (1990) reported higher levels of 

education and income for batterers who completed follow-up surveys 

compared to batterers who did not do a follow-up survey. It is 

unclear, therefore, whether their analysis of treatment effects 

applies to the low SES batterers who failed to complete the survey 

as well as the higher SES batterers who did complete it. 

Finally, batterer treatment programs have serious problems 

with attrition: Many evaluations report that fewer than half of 

batterers assigned to treatment, in fact, completed the program. 

Low treatment completion rates present researchers conducting 

experiments or quasi-experiments with a dilemma. If they compare 

only batterers who complete treatment with batterers not assigned 

to treatment, they are subject to criticisms of "creaming". That 

is, they are comparing the best of the treatment group (the most 

highly motivated batterers) with untreated batterers, thereby 

stacking the deck in favor of finding program effects. On the 

other hand, if all batterers assigned to treatment are included in 

the comparison, yet most failed to complete treatment, they are 

subject to the criticism that their study is biased against finding 

program effects. In other words, program effects would have to be 

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@ very large, indeed, to show up after being diluted by inclusion of 

drop-outs who were not exposed to the treatment (or exposed to a 

lesser treatment "dosage" ) . 

Studies Without a Comparison Group 

.Nan-experimental one group post-test only designs 

At least 15 published studies have used designs which generate a 

single measure of treatment effectiveness: violence fol3owing 

completion of treatment (see Table 1). Ten measured recidivism 

based only upon batterer self-reports. Only four of the fifteen 

studies had substantial sample sizes (which we have arbitrarily 

defined as greater than 100) or lengthy follow-up periods (which we 

have defined as one year or greater). 

Recidivism rates in this group of studies vary widely, from 7% 

to 47% (mean 26%). Interpretation of results is difficult at best 

without a comparison group or pre-test information with which to 

compare outcome measures. 

Non-experimental one group pre-test and post-test designs 

At least seven published studies compared violence among 

treated batterers after program participation to violence levels 

prior to participation (see Table 2). Three of the seven studies 

included both victim and batterer self-reports, but just two had 

follow-up periods of at least a year and none of the studies 

examined police records. Two of the seven studies had sample sizes 

greater than 100. Of the six studies that reported treatment 

attrition rates, four of the studies had attrition rates of 25% or m 

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Table 1: Batterer Treatment Evaluations Using a Post-Test 'Only Design 

..... :...:. .................... 

............ ::::: itt~$..< .................. 

................. .................. ....... :.:.:.:.:.::. .................... 

.:.:::.: ..&.my :. ......... ij :.. ..@g! 

;i;;i;,Si:~;;$ .:.::::,:.:.: .... ...................... 

............ - 

Unknown 'urdy & Nickle (19s I 170 Batterer 6 months 41% 

Batterer 8 months 15% 

Battercr I Year 25% 

Batterer 7 to 21 weeks 22% 

3 

Batterer 4 months 13% 

Battercr 2 months to 3 years 27% 

Battcrer 20 months 35% 

Victim, Police 3 months 19% (Victim) IS% (Police) 

Victim. Batterer 3 months to a few yews 30% (Victim) 18% (Batterer) 

Victim 6 months 47% 

Victim 9 months 33% 

Batterer unknown 19% 

Batterer 1 year 30% 

Batterer 5 months 7% 

Victim 1 year 42% 

Deschner 12 50% (1984) 

Feaze[, Mayers, and 

Deschner (1984) 90 Unknown 

9 idleson, Miller, Stone 

and Chapman (I 985) 

0% 

rleidig, Friedman, an( 

Collins (1985) Unknown Unknown 

Harris Unknown (I 986) 40 

IeMaris and Jackson 

(1 987) 

Leong. Coates, and 

Hoskins (1987) 

Shupe, Stacey & 

Hazlewood (1987) 

83% 53 

67 76% 

148 3 1% 

- 

rolman, Beeman, and 

Mendon (1 987 

68% 

0% 

48 

idlaon and Grusmsk 

(1988) (Study 2) 86 

25% Beninati (I 989) 16 

- 

16% 

30% 

Hambergcr and 

Hastings (1990) 

Johnson and Kanzler 

( 1990) 

106 

687 

rolman and Bhosley 

(1991) 

50% 

- 

99 

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TabIe 2: One Group Pre and Post-Test Design 

- 

50 

.. 

Pre-Test 13.4 All DV acts (Batterer reports) / 

Post-Test 4.6 All DV acts (Batterer reports) 

Pre-Test 2 1.3 All DV acts (Victim reports)/ 

Post-Test 6.1 All DV acts(Victim reports) (For 

- atkdifferences, %05) 

100% (Pre-treatment) 

27% (6 Months) 

(P< .OS) 

9% (4 months) J 

Batterer 8: 

Victim 

6 months to 

3 years 

Dutton (1986) 

Part 1 

4&6 

Months 

Rosenbaurn 

(1986) 

Waldo (1986) 

11 Batterer 18% 

Pre-Test 5.1 DV acts / Post-Test 0.29 DV acts 

(P c .05) 23 Batterer 6 Months lnknowi 

Pre-Test 39% / Post Test 30% 

(Statistical significance not reported) 92 Batterer 14 months 25% 

1 year 

3 months 

I 

Shepard (1987) 

3atterer, Victin 

(Combined 

measure) 

Hamberger and 

Hastings (1988) 

Part 1 

Pre-Test 20.9 DV acts / Post-Test 5.3 DV acts 

(P < .001) 35 0% 

t- Meredith & 53% Physical, verbal & emotional abuse all reducec 

at post-test (% not reported) 125 3atterer, Victim I Bums (1990) 

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less. 

All seven studies reported lower recidivism rates following 

treatment (but results of one study were not statistically 

significant; two studies did not report probability statistics). 

However, with this type of design, reductions in recidivism 

cannot be- .at.tributed. necessarily .to She .effects of .treatment. This 

is true because studies have repeatedly shown that domestic 

violence declines after the police are called, even if nothin& else 

is done. In fact, research suggests that only about a third of 

batterers commit repeat domestic violence within the next six 

months after the police intervene (see, for example, Davis and 

Taylor, 1997; Sherman, 1992; Fagan, Friedman, Wexler, and Lewis 

1984). The post-treatment violence rates displayed in Table 2 also 

average about one-third -- in other words not different than one 

might expect even if the batterers had not undergone treatment. 

Comparing treatment drop-outs versus compl eters Six studies 

compared outcomes between batterers who completed treatment and 

batterers assigned to a treatment program, but who failed to 

complete treatment (see Table 3). Four of the six studies had 

sample sizes under 100. Only two of the six studies had follow-up 

periods of at least one year, and just one included more than a 

single measure of recidivism. 

The most serious flaw in these six studies is that the treated 

and untreated (dropout) groups are almost certainly not comparable 

in complex ways prior to treatment. As pointed out by Palmer, 

Brown, and Barrera (1992), attendance is a confounding factor 

0 

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Victim 

Table 3: Quasi-Experiment (Dropouts Versus Completers) 

Halpem ( 1984) 3 months 18% dropouts! 15% completers (N.S.) 

Police Hawkins & Beauvais 

(1 985) 

6 months 18% Dropouts / 18% completets (N.S.) 

3 

Douglas & Perrin 

(1 987) 

Police 

Edleson and 

Grusznski 

(1988, Studyl) 

29% Dropouts 1 15% Completers 

(No Statistics Reported) 6 months 

Edleson and 

Grusznski 

(1988, Study 3) 

About to 

9 months Victim 

Hamberger and 

Hastings 

Part 2 

(1 988) 

46% Dropouts 132% completeres (P .03) 

81 

Victim 

Batterer, 

106 

1 year 48% Dropouts ! 41% completers (N.S.) 

40 

86 

159 

71 1 1 year 1 47% dropouts / 28% completers (P K.06) Victim, Police 

(Combined 

measure) I I 

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because better attendance is likely an indication of higher 

@ motivation to change, even before treatment. Therefore, 

differential recidivism between program completers and drop-outs 

could be due to motivational differences in the two groups that 

existed prior to treatment. Surprisingly, however, only one of the 

six studies reported significantly lower recidivism rates for the 

completers (four of the other five studies were in the predicted 

direction but either had results that were not statistically -. 

significant or did not include inferential statistics). 

The best use of this group of studies is to describe the 

characteristics of people that drop-out of treatment -- information 

potentially useful to 'program developers to improve batterer 

groups. Results have indicated that those who do not complete 

treatment are more likely to be victims of child abuse (Grusznki & 

Carrillo, 19881, unemployed (Hamberger & Hastings, 1988; 1, 

uneducated (Grusznki & Carrillo, 1988), young (Hamberger & 

Hastings, 19931, psychologically disturbed (Hamberger & Hastings, 

1989; Grusznki & Carrillo, 1988), and substance abusers (Hamberger 

& Hastings, 1990). 

Quasi-Experimental Non-Equivalent Matched Groups 

We found four studies in which batterers mandated to treatment 

by the courts were compared to batterers who received other 

interventions. This group of studies is the first we have examined 

which addressed in a rigorous fashion the issue of whether 

treatment works. There is a notable difference in design details 

. 

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between these four quasi-experiments and the other studies reviewed 

thus far. All four of the studies had sample sizes greater than 

100 (see Table 4). None of the studies relied solely on batterer 

self-reports. All four had follow-up periods of at least one year. 

The first quasi-experiment was reported by Dutton (1986). His 

sample consisted of 100 convicted batterers on probation. He 

@ 

compared 50 batterers who were treated within a cognitivebehavioral group model to 50 batterers who were not designated to 

receive treatment. The treatment group had a 4% recidivism rate 

compared to 40% for the control group based upon police reports. 

However, although Dutton reports that groups did not differ on 

several demographic measures, pre-treatment comparability of the 

groups is highly suspect: The control group was composed of 

batterers whom probation officers did not select for treatment, 

some of whom were explicitly rejected by therapists as unsuitable 

for treatment. The treatment group consisted of only batterers who 

completed the treatment program. Dutton does not report what 

proportion of all batterers assigned to treatment dropped out but, 

based on other work, we have to assume that it was a large 

proportion. 

3 

Chen et al. (1989) conducted a quasi-experiment involving 120 

batterers assigned to treatment by the courts and 101 comparison 

batterers drawn from court calendars who were not mandated to go to 

treatment. (No details are given on how the controls were selected 

or what the outcomes were of their court cases, although the 

authors state that the samples proved to be well-matched 

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Harrell(1991) 

Dobash et a1 

( 1996) 

Table 4: Quasi-Experiment (Matched Control Group) 

348 

3 13 

:hen, Bersani, 

Denton (1989) 

Myers, and 22 1 

batterer & 

victims, 15 

and 29 

IS%scvcrc violence NoTreahnent/20%Trutment(P=N.S.). 

12% physical aggrcrrion No TX I 43% Treatment (PC.0 I) 

7% New DV Charges No Treatment / 19% Trubnnrt (P C .OS) 

. . . . . . . . . 

Police 

Months for 

police 

3& 12 

months 

Police 

7% treated, 10% untreated (court reports 12 months) 

30% treated, 62% Untreated (victim 3 months) . 

33% treated, 75% untreated (victim 12 months) 

No probability statistics provided 

Battered 

Victim 

:Combine( 

measure), 

Police 

victim & 

court 

reports 

40% No treatment / 4% Treatment (P < .001) 6 months to 3 

years 

10% (0.53 DV acts) No Treatment / 

5% (0.35 DV acts) Treatment (P < .OS) 

Peps Attended >73% TX less recidivisim than controls(P<.05) 

3 

Average of 14 

months 

6 months for 

0% 

Jnknow 

24% 

Unknow 

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15 

demographically.). Sixty-three percent of the men assigned to 

treatment completed at least 75% of the required sessions. Chen et 

al. also used a sophisticated data analytic technique (selection 

bias modeling) to deal with the potential non-equivalence of groups 

prior to treatment inherent in non-randomized experiments. They 

found that, after an average of 14 months, 5% of batterers assigned 

to treatment had been rearrested compared to 10% of controls. The 

main effect of the treatment variable was not statistically 

significant, although the authors noted that batterer3 who 

completed at least 75% of the requisite sessions had significantly 

lower rates of recidivism than controls. 

Harrell (1991) studied 227 batterers, 115 of whom were ordered 

to treatment by judges. (She does not specify what court outcomes 

of the untreated group were.) Her attempt to obtain equivalency 

between those treated batterers controls hinged on a quirk in the 

court she studied. She noted that treatment program referrals came 

almost exclusively from a small group of judges; other judges 

seldom mandated treatment for batterers. Therefore, she drew her 

comparison group from the caseloads of judges who seldomly referred 

to the treatment program. However, her plan did not work as she 

had intended. Harrell found three important and statistically 

significant differences between treated batterers and controls. 

(The former were more likely to be married to their partners and 

employed, and less likely to have a criminal record). While she 

controlled for these variables in her analysis of recidivism 

effects, it is quite possible that there were additional, 

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unmeasured differences between the groups. 

Harrell’s analysis included only batterers in the treatment 

group who actually completed treatment. Comparisons of recidivism 

were based on a combined measure of the victim and perpetrator 

reports of violence six months after case disposition. In 

addition, police records were reviewed 15-29 months after case 

disposition. Surprisingly, a significantly larger percentage of 

those in the treatment group committed new violence than those in 

the control group for two of three measures that she reports. 

(The third measure is in the same direction, but not statistically 

significant.). For example, 7% of the control group and 19% of the 

treatment group were charged with new domestic crimes. While 

Harrell’s study may be limited in its ability to distinguish 

between selection effects and treatment effects, it certainly adds 

controversy to the debate about the efficacy of treatment programs. 

Recently, Dobash, Emerson-Dobash, Cavanagh and Lewis (1996) 

reported on a quasi-experiment evaluating a treatment program in 

Great Britain. Dobash et al. examined 256 domestic violence cases 

from sheriffs’ courts in Scotland in which defendants were 

3 

sentenced to batterer treatment or to another sentence (probation, 

court supervision, or prison). Few details are given about how the 

control group was selected, but the authors note that batterers in 

the treatment group were significantly older and more likely to be 

employed than batterers in the control group. (These differences 

are reminiscent of pre-treatment differences in Harrell’s study.) 

It is not specified whether Dobash, et. al. included in their 

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analyses all batterers assigned to treatment, or only those who 

completed treatment. According to court reports at 12 months 

follow-up, 7% of the treatment group recidivated compared to 10% of 

the control group: No statistical tests were reported to indicate 

whether the difference was significant. Data from victim surveys 

indicated that half as many batterers assigned to treatment 

committed new violence at three or 12 months as controls. (These 

two comparisons are reported to be statistically significant, 

although no specific information is provided.) However, the 

success rate for interviews was low: Dobash et al. interviewed only 

43% of the victims at the first follow-up interview, 34% at the 

second interview, and 25% at the third interview. 

Randomized Experiments 

As pointed out by Palmer et al. (1992), quasi-experiments on 

batterer treatment cannot be relied upon to produce unbiased 

estimates of the effects of treatment. This is true because we 

cannot know whether batterers assigned to treatment and controls 

are equivalent prior to application of the treatment. In some 

quasi-experiments (such as the Dutton, 1986 or Harrell, 1991 

studies), we know for certain that selection bias favored finding 

treatment effects (because the control group was comprised of 

batterers more prone to recidivate than those in the treated 

group). 

It can be argued that initial differences between groups can 

be controlled statistically, but this is only true if all relevant 

initial differences are known to researchers. For example, a 

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researcher may discover pre-treatment differences in employment, 

marital status, and criminal history between those assigned to 

batterer treatment and controls, and these differences may be 

statistically controlled in analyses. However, groups may well 

have differed on less tangible and more fundamental factors such as 

emotional maturity as well. If such factors are not controlled 

(because they are not known) and they are correlated with outcome 

measures, then the results of the study are uninterpretable. The 

safest way to ensure that estimates of sample means are unbiased is 

3 

through random assignment of batterers to treatments. 

Palmer et. al. conducted the first experiment with random 

assignment to a true no treatment control group. The number of 

subjects in the experiment was far smaller than one would expect to 

need to detect treatment effects: Fifty-nine probationers were 

assigned using a "block random" procedure to either a ten-session 

psychoeducational group (combining group discussion with 

information) or a no treatment control group: Participants were 

assigned to treatment if a new group was to commence within three 

weeks; otherwise they became part of the control group. In only 

two cases was a defendant assigned to the control condition 

reassigned by court officials to the treatment condition. 

Attrition was kept within a respectable range: 70% of the men 

assigned to treatment attended at least seven of the required 10 

sessions. 

It is significant that this is one of the only studies to 

compare all batterers assigned to treatment (not just those who 

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completed treatment) with controls. Palmer and her colleagues 

examined police reports six months post-treatment and found 

recidivism rates (domestic physical abuse or serious threats) for 

the treatment group to be just one-third that of the control group 

(10% compared to 31%). Even with the small N, this difference was 

statistically significant. While Palmer et. al. attempted to 

generate additional violence measures from surveys of interviews 

and batterers, low response rates combined with a small N precluded 

any analysis of recidivism based upon interview data. 

-. 

Two additional randomized experiments are in progress. 

Dunford (1997) is in the final stages of comparing treatment 

outcomes for 861 legally married Navy couples in which physical 

abuse had come to the attention of Navy authorities. These cases 

were randomly assigned to one of four treatments, including (a) 26- 

week batterer treatment (based on a cognitive/.behavioral model), 

(b) 26 weeks of couples counseling, 0 rigorous monitoring 

(including monthly calls to victims and semi-annual police record 

checks), and (d) establishing a safety plan for victims. The 

safety planning was intended by the investigators as a no-treatment 

control against which to compare the effects of the other three 

treatments. (Safety planning was given to victims in each of the 

other three conditions as well. ) This would seem to be a fairly 

good no-treatment condition, in so far as the men in this condition 

received no intervention. Victims and batterers are being 

interviewed every six months over a period of two years. Feder 

(1996) has assigned batterers placed on probation to either a 26- 

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week educational batterer program based on the Duluth model or a 

control group not mandated to treatment. Multiple measures of 

recidivism will be assessed (victim, batterer, police records, 

probation records) for six months and one year. 

Purposes of the Present Studv 

We sought to add to the incipient literature on randomized 

studies of batterer treatment. Although any form of design can be 

criticized, we concur with Fagan (1996) that randomized experiments 

entail less serious problems than other designs. A properly 

executed randomization process is the only way to ensure that 

treatment effects are not confounded with pre-existing subject 

characteristics. Our study adds to the literature on randomized 

3 

experiments in several important ways. 

Unlike the sites of the Palmer and Feder experiments, 

batterers in the site of our study were mandated to treatment by 

judicial order (in the sites of the other two studies, orders to 

treatment were made by probation departments). This difference has 

implications for the kinds of batterers studied. The Palmer and 

Feder studies had a wide sampling frame, including all or most 

batterers sentenced to probation, regardless of the batterers’ 

willingness or unwillingness to enter into treatment. In our 

study, batterers were only eligible for inclusion if all parties to 

the case (prosecution, defense, and judge) agreed that treatment 

was appropriate. Such agreement was forthcoming in a small 

percentage of cases, most often because the defense refused to 

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21 

agree to treatment. Thus, our results are less easy to generalize 

to larger groups of batterers than the results of the Palmer and 

Feder experiments. On the other hand, because all batterers 

included in our sample had to have agreed to treatment, our study 

presumably did not include batterers who were unmotivated. Of 

course, all participants were court-mandated; they did not 

volunteer for treatment of their own volition. Still, it is common 

knowledge in Brooklyn Criminal Court that misdemeanor batterer 

defendants are not facing jail time, and participants in tregtment 

certainly knew from counsel that they were choosing the batterer 

program over another alternative to incarceration. The point about 

motivation is key, since it has often been argued (see, for 

example, Rosenfeld, 1992) that treatment cannot be expected to work 

for individuals there against their will. 

W 

The difference between our study and others in how batterers 

were mandated to treatment also has implications for comparison 

groups. The Palmer and Feder studies compared probationers 

assigned to treatment to probationers who had similar supervision 

conditions except for the treatment mandate. In other words, 

treatment was compared to the absence of treatment. In contrast, 

our work compares batterers assigned to treatment to batterers 

assigned to a community service program irrelevant to the problem 

of violence. The comparison between batterer treatment and an 

irrelevant treatment is appropriate for judicially-mandated 

treatment referrals (since all convicted batterers must receive 

some sentence), just as the treatment/absence of treatment 

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comparison is appropriate for probation-mandated referrals. 

The Palmer experiment found a significant effect of treatment 

although the sample size was surprisingly small because the 

treatment effect size was extraordinarily large. Our work planned 

sample size based upon an examination of effect sizes described in 

the literature. Thus, the design contains sufficient power into to 

provide for adequate tests of the effects of treatment upon several 

indicators of violence and attitudes. 

Due to fortuitous circumstances, we wound up splitting our 

treatment sample into two subsamples distinguished by density of 2 

treatment sessions. All batterers randomly assigned to treatment 

were mandated to attend 39 hours of psycho educational group 

treatment based upon the Duluth model. However, some batterers 

received the 39 hours in 26 weekly sessions while others received 

it in longer biweekly sessions for 8 weeks. The former treatment 

model maximized time that batterers remained in treatment while the 

latter reduced the chances that batterers' initial motivation would 

0 

flag over time. 

Finally, our work included both short-term (6-month postsentence) and intermediate-term (12-month post-sentence) follow-up 

on treatment outcomes. Short-term outcomes are important to assess 

because any effects of treatment may be short-lasting. We know 

that the likelihood of violence declines as time passes from the 

time a domestic complaint is made to the police (see, for example, 

Davis and Taylor, 1997). Any early differences in violence due to 

treatment might therefore disappear as violence in the control 

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group came down over time. Longer term follow-up is also important 

to determine whether any short-term effects of treatment hold up in 

the months after batterers are no longer attending treatment and 

under court control. 

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11. METHOD 

Overview 

The stuhy was conducted using a true experimental design in 

which 376 criminal court defendants were mandated to attend a 40- 

hour batterer treatment program or to complete 40 hours of 

community service. The random assignment was made at sentencing, 

after all parties (judge, prosecutor, and defense) had agrfed to 

batterer treatment, if it was available based on the random 

assignment process. 

Batterers and victims were interviewed about new violence on 

three occasions: At the time of sentencing, six months after 

sentencing, and twelve months after sentencing. Official data on 

new complaints to the police and new arrests were gathered six and 

twelve months after sentencing. 

Cases Included in the Studv 

The sampling frame consisted of spousal assault cases in Kings 

County (New York) Criminal Court in which all parties had agreed in 

principal to accept batterer treatment, if the defendant was 

accepted by the Alternatives to Violence (ATV) program. This 

proved to be a small percentage of cases adjudicated within the 

course of intake. Intake began on 2/19/95 and ran through 3/1/96. 

During that time, 376 cases were taken into the sample, about 1- 

1/2 cases per day. During the same period, roughly xxx??? domestic 

violence cases were adjudicated (i.e., had dispositions other than 

24 

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dismissal), or about yyy??? per day. 

In nearly two-thirds (64%) of the cases in the study, 

defendants were charged with 3rd degree assault (a class A 

misdemeanor). An additional 19% were charged with felonious 

assault (although pleas would be to misdemeanor charges). The 

remaining 17% were charged with violating restraining orders, 

menacing, harassment, and other charges. Court dispositions on 

cases in the sample were most commonly guilty pleas followe2 by a 

conditional discharge (68% of the sample) or probation (8% of the 

sample). Twenty-three percent of the cases were adjourned in 

contemplation of dismissal (a form of pretrial diversion in which 

cases are dismissed and records expunged if defendants avoid arrest 

and adhere to judicial conditions for six months). Conditional 

discharges and probation place defendants under court control for 

a period of one year, compared to a period of six months for most 

adjournments in contemplation of dismissal. 

Batterers were all males with a median age of 31 years. The 

sample contained a plurality (36%) of African-Americans, with 

substantial numbers of men from Latino (28%) and West Indian (21%) 

origins as well. Sixty-two percent had graduated high school and 

just 4% had graduated college. Only about half (54%) of the men 

reported being employed full time, and just 40% had been 

continuously employed during the past year. Roughly one-third 

(36%) reported household income under $10,00O/year, while 26% 

earned between $10,000 and $20,000, and 37% $20,000 or more. 

Victims all were females with a median age of 29 years. Six 

25 

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1 in ten victims (59%) were black, 30% were Latino, and 9% white. 

The proportion of victims who graduated high school (66%) was 

comparable to the proportion of high school graduates among 

batterers reported above. Fewer victims, however, were employed 

(38%) and a large proportion (43%) received public assistance. 

Surprisingly, just 9% of the victims reported the batterer as their 

primary source of assistance. Victims were poorer than batterers, 

with close to half (46%) reporting household incomes of under 

$10,00O/year. 3 

Victims and batterers had been together a median length of 

time of 5-1/2 years. On average, violence had begun occurring by 

two years into the relationship. About two-thirds of victims and 

defendants lived together at the time of arrest (70% according to 

batterer interviews/ 62% according to victim interviews). Most 

batterers in the sample were in current romantic relationships with 

the victims either as legal spouses (37% according to batterers/ 

33% according to victims), live-in boyfriends (19% according to 

a 

Victim racial profiles differ from defendant ethnic profiles reported 

above because the questions were asked somewhat differently on the respective 

interviews. The proportion of victims categorized as “black” corresponds 

closely to the proportions of defendants categorized as “African-American” 

(36%) plus the proportion categorized as ’west-Indian” (21%). 

26 

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batterers/ 11% according to victims), or live-out boyfriends (9% 

according to batterers/ 6% according to victims). Victims and 

batterers were no longer in a current relationship (33% according 

to batterers/ 49% according to victims). A large majority of 

batterers had children in common with the victim (63% according to 

batterers/ 79% according to victims). 

Sixty-two percent of victims said that they had called the 

police in the past because of their perpetrator's abuse. Forty- 3 

eight percent of the victims had filed a police complaint against 

their perpetrator in the past. Thirty-four percent of the victims 

had an order of protection against their perpetrator in the past. 

Twenty-three percent of the victims stated that the perpetrators 

had been arrested in the past for abusing them. According to 

official records, 39% of batterers had been arrested previously for 

any type of crime. 

Treatments 

There are two ways to conceive of a control treatment for 

assessing the effects of batterer treatment programs. One is to 

compare batterer treatment to the absence of treatment. For 

example, when batterer treatment is left by judges to the 

discretion of probation officers, assignment to treatment or no 

treatment can be made at the time of probation intake. This is the 

method being used in Feder's current study for NIJ. 

That option was not available to us since, in New York City, 

probation for misdemeanor spouse abuse charges is very rare: Judges 

27 

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are the ones who mandate batterers to treatment, and completion of 

0 the program is normally the only condition of plea arrangements. 

It clearly was not possible to suggest to criminal justice 

officials that they let selected defendants simply walk with no 

sanctions. Therefore, we needed an alternative sanction for the 

control group -- a sanction which was irrelevant to the battering 

problem that resulted in the men's arrest. Community service, as 

defined below, was such a sanction and criminal justice officials 

agreed to use it as an alternative to ATV for men designated by 3 

researchers as controls. All participants in our experiment were 

assigned to receive either 40 hours of group batterer treatment or 

40 hours of community service. 

Batterer treatment The batterer treatment program was Victim 

Services' Alternatives to Violence (ATV), based upon the Duluth 

model. The original model mandated 26 weeks of attendance at a 

weekly group meeting that lasted one hour. The course was rooted 

in a feminist perspective and assumed that domestic violence is a 

by-product of male and female sex roles which result in an 

imbalance of power. The curriculum included: Defining domestic 

violence, understanding the historical and cultural aspects of 

domestic abuse, and reviewing criminal/legal issues. Through a 

combination of instruction and discussion, participants were 

encouraged to take responsibility for their anger, actions, and 

reactions. Sessions were conducted in either English and Spanish 

by two leaders, one male and one female. 

ATV had changed its format just at the time that the 

28 

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experiment began, expanding the number of required hours from 1-1/2 

hours once a week for 12 weeks to 1-1/2 hours once a week for 26 

weeks. The change was made to conform with New York State 

guidelines and was in line with national trends. However, the 

lengthened program became a sore spot for Legal Aid Society 

attorneys who defend the vast majority of defendants in Brooklyn 

Criminal Court judged to be indigent. While Legal Aid 

administrators had pledged cooperation (and, indeed, made good on 

that pledge), staff attorneys began to advise their clients against 

involvement in the new version of the ATV program. Intake glowed 

to the point that we would have been unable to complete intake 

within any reasonable time frame. At a meeting with Legal Aid 

staff attorneys we realized that their objections to ATV stemmed 

from the increased time that their clients were under court control 

and from the increased session fees that their clients paid over 

the course of 26 sessions. 

It became clear that, if we were to complete intake, we would 

have to accommodate the Legal Aid attorneys' objections to the 26- 

week batterer treatment program. Therefore, with the help of ATV 

administrators, we designed a new 8-week format through which 

participants could complete the same 40 hours of group time through 

bi-weekly 2-1/2 hour sessions with lower fees per session. The new 

format began to be offered after the first 129 participants had 

been assigned to 26-week groups. From 8/15/95 until the end of 

intake, defendants were offered a choice between 8-week and 26-week 

formats. In practice, no one chose the 26-week option once the 8- 

29 

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week groups became available. Thus, the final 61 ATV participants 

were assigned to the 8-week groups. 

Community service Defendants rejected by lottery from 

batterer tr'eatment were mandated by judges to participate in 70 

hours of community service. Typically, the service was performed 

over a two-week period. For offenders who were employed, flexible 

hours were arranged over a two-month period in order that they 

could continue their jobs. Participants were assigned to work on 

renovating housing units, clearing vacant lots to make way for 

community gardens, painting senior citizen centers, and cleaning up 

playgrounds -- all activities which would not be expected to impact 

on abusive behavior. In the course of their service, participants 

were given education about drugs and HIV. Interested individuals 

were also referred to drug, HIV, or employment counseling programs. 

3 

Participants in both batterer treatment and community service 

programs were expelled from the programs if a pattern of nonattendance developed (for ATV, three misses constituted grounds for 

dismissal from the program). For the men assigned to batterer 

treatment, such cases were referred to the prosecutor's office for 

action. At the discretion of the district attorney's office, 

delinquent cases were returned to the court calendar and new 

sentences could be imposed. In practice, few cases were actually 

restored to the calendar because the period of court supervision 

typically was drawing to a close by the time a clear pattern of 

non-compliance was established and a restoral request was 

30 

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completed. 

Follow-up on delinquents was more reliable for the community 

service group. The organization running that program had the 

ability to place cases of delinquents on the court calendar 

themselves, rather than recommending to the prosecutor that cases 

be restored. If the court issued an arrest warrant for noncompliance, the community service program had enforcement staff who 

executed the warrants. 3 

Assianment Process and Case Intake 

Cases were drawn from three of eight post-arraignment parts in 

Kings County Criminal Court. Two of the parts were specialized 

domestic violence parts. The third was the jury trial part where 

domestic violence and other cases were transferred if a negotiated 

disposition could not be reached. At the point at which judge, 

prosecutor, and defense had reached agreement on batterer treatment 

as an appropriate disposition, the prosecutor called the ATV office 

in the court building. Either the ATV intake person or a research 

assistant picked up the defendant in court and brought him to the 

ATV office for an intake interview. 

@ 

Upon completion of the interview, the defendant's name and 

case identifier were entered onto the next line of a logbook. Each 

line of the book had a pre-assigned treatment designation (batterer 

treatment or community service) determined through the use of a 

random number table. The use of the log with pre-determined 

treatment assignments and the presence of a research assistant on 

31 

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the three busiest days of the week helped to ensure the integrity 

of the random assignment process, Defendants assigned to batterer 

treatment were given a start date (usually within a week of intake) 

and directions to the class. 

The defendant was accompanied back to the courtroom and the 

prosecutor informed of the lottery assignment. The prosecutor 

informed the judge who then accepted a disposition consistent with 

the assignment. In 28% of control cases judges overrode the 

lottery decision to deny batterer treatment and mandated the ATV 

program for defendants who had been assigned to community service. 

There were no judicial overrides of cases randomly assigned to the 

ATV program. 

Fo11ow-UD Measures and Rationale 

The literature suggests that batterer treatment is designed to 

reduce violence against women by changing batterers' cognitive 

understanding about the roles of men and women in society and in 

relationships. Programs also aim to change batterers' attitudes 

toward the legitimacy of using violence against family members and 

to teach batterers ways to resolve interpersonal conflicts without 

resorting to violence. 

Because the most important outcome of treatment is reduction 

of violence, we included several measures of new violence in 

victim-batterer relationships. The violence measures (described 

more fully below) were: new arrests; new crime reports (which may 

or may not result in an arrest); and self-reports of violence by 

32 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

This document is a research report submitted to the U.S. Department of Justice. This report
. 0 victims and batterers. These same indicators have become commonlyused in studies which track households where domestic violence 

occurs, for example, in NIJ's SARP research (see, for example, 

Fagan, Garner, and Maxwell, 199??). The three violence indicators 

do not always behave in similar ways (see, for example, Davis and 

Taylor, 19971, so it i-s important to capture a variety. Each of 

the violence measures was captured at 6 and 12 months after the 

time that batterers were sentenced. Victim and batterer "selfreports were obtained through (primarily) telephone interviews. 

Crime report and arrest data were obtained from official records. 

In addition to capturing information on new violent acts, the 

interviews also assessed attitudinal and cognitive behaviors among 

batterers and victims. For both groups we measured attitudes 

toward violence in the family and conflict resolution skills. We 

also measured for both batterers and victims whether their 

0 

cognitive styles tended toward internal or external locus of 

control. That is, did they believe that they could influence 

events or did they believe that things happened to them? It seemed 

plausible that, if batterer treatment succeeded in engendering in 

batterers a greater sense of responsibility for their actions, they 

would become more internal on locus of control. Finally, the 

interview schedules included for victims only measures of 

psychological adjustment. If treatment of the batterer led to 

changes in the way that they acted toward their partners then, we 

believed, that women's self-esteem and sense of well-being might 

33 

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Interview Methodoloav 

We attempted interviews with defendants and victims on three 

occasions: (a) at case intake (date of court disposition), (b) six 

months after intake, and Q twelve months after intake. Interviews 

with batterers were conducted in person in the court building just 

prior to assigning them to either batterer treatment or community 

service. In subsequent interviews with batterers and 3 all 

interviews with victims, telephone was the modality of choice. 

Because we considered the victim interviews more accurate than 

batterer interviews for assessing new violence, we put special 

efforts into interviewing victims. When telephone attempts failed, 

we sent teams of interviewers to victims’ homes. If the home 

interview attempts also failed, we mailed letters offering first 

$25 and then $50 for completion of an interview. In the third 

interview wave for victims we turned over 70 difficult cases to a 

licensed private investigator as a last resort. The private 

investigator used available computer databases to track victims who 

had moved and provide us with current addresses. He did not 

confront victims or their acquaintances, and interviews for women 

he located were conducted by our staff over the phone. Ultimately, 

this additional tracking methodology added virtually nothing to the 

interview success rate. 

Completion rates Our completion rate with victims was 

50% for the first interview, 46% for the second interview, and 50% 

for the third interview. First interviews with batterers were 

34 

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obtained with 95% of the sample because interviews were obtained 

when defendants were present at intake in court for the treatment 

program. Subsequent completion rates were 40% for the second 

interview and 24% for the third interview. The fact that attrition 

among victim interviews was substantially lower than among 

batterers results from the extra lengths (incentives, in-person 

visits) to which we went in order to obtain the victim interviews. 

The refusal rate for both victims and batterers was quite low 

(7% and 13%, respectively). The primary reason for not completing 

interviews with victims and batterers was inaccurate or outdated 

information obtained from prosecutor files. We had a core group of 

23% of victims whom we were unable to contact on any of the three 

interview occasions. In many of these cases, we found out 

definitively that the victims had moved, and we suspect that this 

was the case with most of this group. We have found in research in 

other cities as well (Davis, Smith, and Nickles, 1997) that courtinvolved domestic violence victims are a highly transient 

population with marginal attachment to addresses. Many of those 

staying with the batterer or with family members at the time of 

arrest move within a short period of time thereafter. 

3 

Interview completion rates did not vary significantly by 

treatment. Batterer completion rates for experimentals and 

controls were 94% and 96% at time 1; 42% and 38% at time 2; and 28% 

and 20% at time 3. Victim completion rates for experimentals and 

controls were 51% and 50% at time 1; 41% and 50% at time 2; and 52% 

and 48% at time 3. 

35 

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Interview rates did vary, however when broken down by some 

(I) case characteristics. We examined variation in victim and batterer 

interview completion rates according to batterer age, education, 

income, employment status, ethnicity and prior arrests. (We used 

batterer rather than victim characteristics because the former were 

available for virtually the entire sample and because batterer 

characteristics have been the primary control variables used in 

other research on interventions to prevent domestic violence.) In 

addition, we examined variation in victim and batterer interview 

3 

rates according to whether the parties were involved in a current, 

versus an ex-, romantic relationship. We uncovered no significant 

differences in interview completion rates for either victims or 

batterers as a function of batterer age, income, employment status, 

education, prior arrests, or nature of victim/batterer 

relationship. Neither was there a significant difference in 

batterer interview completion according to ethnicity. However, 

ethnicity was correlated with completion of victim interviews: 

Interviews were completed with victims in 62% of the cases in which 

batterers were black compared to 76% of the cases in which 

batterers were non-black (the vast majority of these were non-black 

latinos) .2 

Interview content Measures on victim and batterer interviews 

included (a) background information (violence histories and 

demography); (b) measures of new violence; 0 beliefs about domestic 

'Chi-square = 7.99, p < .01. 

36 

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violence; (d) conflict management skills; and (e) locus of control. 

In addition, victims were administered a short scale measuring 

well-being. Interviews at the three time points were identical 

except for the omission of background information on second and 

third interviews. 

a 

A) Backaround information: (1st interview only) 

We assessed violence history in the current relationship 

between victim and batterer and violence outside of 3the 

current relationship perpetrated by batterers and experienced 

by victims. We also collected limited demographic data (age, 

ethnicity, marital status, socio-economic status). 

B) Measures of recidivism: 

To assess frequency and severity of violence, we employed 

Harrell's (1991) adaptation of the Conflict Tactics Scale 

(Straus, 1979). Harrell's scale measures the frequency of a 

range of 11 different violent acts. 

The reference period for the scale was the previous two 

months (as opposed to the previous six months for the 

criminal justice measures). We reasoned that, if treatment 

did make a difference, it would take some time to have its 

effect. Thus, asking victims to report at the six month 

interval about the entire period would inevitably include 

violent incidents committed shortly after cases were assigned 

to treatment. The two month reference period we decided upon 

ensured that any violence reported would have occurred after 

batterers had been in treatment for a good length of time. 

37 

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C) Beliefs about domestic violhce 

Part of the treatment program curriculum was to encourage 

batterers to recognize the rights of women not to be abused 

and to reevaluate the rights of men to use violence to control 

women. To measure generalized beliefs of batterer and victim 

about the legitimacy of spouse assault, we used a scale based 

on the "Inventory of Beliefs about Wife Beating Scale" 

(Saunders, Lynch, Grayson and Linz, 1987). We began 

pretesting using the Saunders, et. al. scale intact. Hoyever, 

we soon discovered that many items had little variation. That 

is, batterers overwhelmingly endorsed the socially desirable 

choices. These items were dropped and others added, making up 

a new scale of ten items. 

D) Conflict manaaement strateaies 

We assessed conflict resolution skills of victims and 

batterers using Harrell's (1991) measure of Conflict 

Resolution Skills. Harrell's scale is loosely based on Form 

N of the Straus Conflict Tactics Scale. 

E) Locus of control 

To assess the degree to which victims and batterers 

perceived outcomes as contingent upon their actions, we 

originally attempted to employ Rotter's (1966) InternalExternal Locus of Control Scale. However, in pretesting, we 

discovered prevalent comprehension problems with the Rotter 

scale. Therefore, we drew 12 items from the 40-item NowickiStrickland Internal-External Control Scale (Nowicki and Duke, 

38 

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1974). This scale is an adaptation of the Children's NowickiStrickland I-E Scale, and is thought to be less difficult than 

Rotter's scale. The items selected were those that seemed 

most relevant to spouse abuse (e.g., 'Do you feel that most of 

the time it just doesn't pay to try hard because things never 

work out right anyway?" or 'Most of the time do you find it 

hard to change a friend's mind? " ) . 

F) Well-Beinq (Victims only) 3 

To measure well-being of victims, we used the Life 

Satisfaction (Index B) (Neugartin, Havighurst, and Tobin, 

1961). The scale contains 12 items, each with three ordered 

response options. 

G) Self-esteem 

We used the Rosenberg Self-Esteem Scale:(Rosenberg, 1979) 

to gauge self-perceptions of victims. This 13-item scale asks 

individuals to rate their extent of agreement (from strongly 

agree to strongly disagree) with a series of statements about 

themselves, such as "I am able to do things as well as most 

other people. 'I 

Information Collected from Criminal Justice Records 

Computerized records of the Criminal Justice Agency (CJA) and 

of the New York City Police Department (NYPD) were searched to 

determine if the batterer was arrested for a new crime or if a new 

crime report was filed during the study period. CJA's database of 

New York City arrests was accessed via the court docket numbers of 

39 

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cases in or sample. Docket numbers led us to defendant NYSID 

(state criminal identification) numbers, which we used to determine 

if the defendant had had subsequent arrests during the 12 months 

0 

since sentencing on the sampled case. (All CJA record checks 

covered at least 12 months, and some covered as many as 26 months.) 

When new cases were found, the arrest date and charge were 

recorded. In addition, the docket number was used to search the 

district attorney's computer database to determine whether the 

victim in the new case was the same as the victim in the original. 

Because the searches were conducted using ID numbers, we are 

J 

confident that our information on new arrests is highly accurate. 

The computerized records of the NYPD were searched to 

determine whether new crime complaints had been filed against the 

defendant since sentencing in the original case. These searches, 

conducted by NYPD personnel, were conducted using batterer names 

and incident addresses. Therefore they were subject to errors in 

spelling of batterer names or street names in address checks. 

Also, each police precinct maintains its own database. When 

batterers commit a crime outside of their home precinct, their home 

precinct is supposed to receive a record, but we do not know how 

reliably information is transferred across precinct boundaries. 

When hits (new incidents) were found, officers recorded the dates 

of new incidents, the nature of the complaint, and whether the 

complaint involved the same victim as the original case. As a 

result of these shortcomings, we expect that the NYPD data 

undercounted violence reported to the police. We have no reason to 

@ 

40 

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believe that the extent of undercatinting would vary according to 

experimental treatment. 

We combined the CJA and police data into one measure of new 

criminal justice involvement in the form of arrests or crime 

complaints. This parallels the method used by Maxwell (1998) in 

the most recent reanalysis of data from NIJ’s SARP experiment. 

B 

41 

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111. TREATMENT EFFECTS 

Analvsis Plan 

Our initial decision in data analysis was whether to analyze 

according to the original two-group design, or to capitalize on the 

fact that we actually had three treatment groups (8-week, 26-week, 

control). We examined the data both ways, and discovered that 

there were substantial differences in outcomes between the two 

different lengths of batterer treatment. Therefore, we have chosen 

to present the data broken down into three-group comparisons. 

However, the same analyses reported here were conducted as well 

using two-group comparisons with essentially the same pattern of 

differences between control and treatment groups. 

3 

Our initial design called for examining treatment effects six 

months after sentencing. This interval was chosen to coincide 

roughly with the end of the 26-week program for subjects assigned 

to the batterer treatment condition. We reasoned that any 

treatment effects would be maximal after subjects received the full 

treatment "dosage". However, effects might decay with the passage 

of time after program completion. This could happen either because 

the men assigned to batterer treatment became more violent as time 

since program completion increased or because control subjects 

became less violent as more time passed since the incident that led 

to their arrest. 

During the course of our investigation, we were fortunate to 

42 

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receive additional funding from NIJ to enable us to follow subjects 

up to one year post-sentence. This allowed us to determine if any 

effects of batterer treatment that were observed immediately upon 

completion held up over time. Accordingly, we have divided our 

analyses into short-term (through 6 months post-after assignment to 

treatment) and long-term (through 12 months after assignment to 

treatment) effects. 

Comparisons Evaluations of batterer treatment pose a 

challenge for researchers in part because many of those who start 

3 

treatment programs do not finish them. This was true for our 

sample as well (see section below on attendance). The temptation 

in such instances is to compare only those who complete treatment 

(and therefore get the full "dosage") to a comparison group. 

However, we followed the example of the SARP investigators in our 

decision to analyze cases according to the treatment to which they 

were assigned rather than according to the treatment that they 

0 

received. This is the course most frequently recommended in both 

the criminal justice literature and medical literature on clinical 

trials, although "crossovers" result in loss of statistical power . 

when "analyzing as randomized" (Weinstein and Levin, 1989) . 

However, there are two compelling arguments for our approach. 

First, the alternative (analyzing cases according to the 

actual treatment they receive) runs a serious risk of defeating the 

purpose of randomizing in the first place, i.e. creating groups of 

cases equivalent prior to treatment. In our case, the crossovers 

were created because judges intervened in the random assignment 

43 

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process. Their abrogation of the random assignment in a minority 

of cases clearly was not a random process. Therefore, it is likely 

that including such cases in the "treated" group would obviate the 

initial equivalence that we had sought through randomization. A 

second argument for analyzing as randomized was made by Gartin 

(1995). He argues that, in policy studies such as ours, the issue 

is not the effect of the treatment per se, but the effect of a 

policy to apply treatment. 

Sherman (1992) proposes following the "analyze as randomized" 

dictum as long as the proportion of treatment crossovers does not P 

exceed the proportion of cases with negative outcomes. Our study 

has a 14% crossover rate due to judicial overrides of random 

assignments to the control group. This is slightly higher than the 

one year combined arrest rate of 11% (our most conservative outcome 

measure), but below the one year combined crime report rate of 17% 

and the one year victim reports of 19%. 

Appendix A presents a comparison of characteristics and 

violence outcomes for the judicial overrides versus the rest of the 

controls. None of the differences approached statistical 

significance, although it must be kept in mind that the number of 

override cases was small (n=52). There was a substantial 

percentage difference between override and other controls in the 

proportion arrested for new crimes against the victim within 12 

months of sentencing (21% versus 12%, respectively, p=.14). 

Assuming that treatment reduces violence, the effect of our analyze 

as randomized strategy is to reduce the magnitude of treatment 

44 

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effects, i.e. to make the statistical tests more conservative and 

rejection of the null hypothesis less likely. 

Statistical tests At each of the two time points we 

conducted identical sets of analyses. We began by examining two 

measures of prevalence: (a) new criminal justice incidents 

involving the same victim and (b) new reports of violence made by 

victims during the course of research interviews. The basic 

prevalence comparisons between the experimental conditions were 

done as simple bivariate comparisons. 

The prevalence tests were followed by two additional tests on 

each measure at both time points. The first test was either a 

Poisson or a negative binomial regression, testing whether the 

distribution of failures (i-e., cases in which new violence 

occurred) differed according to treatment. Poisson and negative 

binomial regression were developed specifically for the kind of 

distribution of failures that we observed, i.e. a large majority of 

the sample did not fail at all during the time observed, some 

failed once, fewer failed twice, and a handful failed more often. 

This kind of highly skewed distribution seriously violates the 

normality assumption of analysis of variance, even with log or 

other transformations of the data. 

The second test was proportional hazard analysis, examining 

differences between treatment conditions in elapsed time to first 

failure. In other words, even if no differences were observed 

between treatments in the proportion or frequency of new violent 

incidents, it is still possible that one group failed earlier than 

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another. 

Finally, for each of' the two time points, we examined 

treatment effects upon measures of cognitive changes, including 

conflict resolution skills, beliefs about domestic violence, and 

locus of control. These tests were performed using analysis of 

> 

variance. 

Introduction of covariates In the negative binomial and 

proportional hazard tests, we added to the model a set of 

covariates in addition to the treatment variable. The introdfiction 

of covariates in analyzing data from a randomized experiment is 

unusual and, strictly speaking, is not necessary: Randomization 

ought to ensure that other measures, known or unknown, that are 

related to the failure measure, such as the suspect's age or prior 

criminal record, are similarly distributed across the treatment 

groups and therefore will not bias the basic experimental treatment 

comparisons described above. In our case, this goal seems largely 

to have been achieved (see section on pre-treatment comparisons 

between groups in the last chapter). 

However, introducing covariates is increasingly common even in 

analyzing data from randomized experiments (Patel, 1996; Armitage, 

1996). There are several reasons why this is the case. First, 

statistical controls for other factors tend to improve the 

precision of the treatment comparisons and correct for any major 

imbalance in the distribution of these measures across treatments 

that may have occurred by chance (Armitage, 1996). Second, since 

the suspects assigned randomly to the same treatment group are not 

46 

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exactly alike, statistical controls can address the natural 

variations between suspects within each treatment group (Gelber & 

Zelen, 1986). Third, while an experimental analysis typically 

tests for only the average effects of treatment across all 

subj ec ts , whatever their characteristics, additional 

nonexperimental hypotheses can specify other expected direct 

effects, like age on the outcomes, and how treatment effects may 

vary across dimensions of other uncontrolled extraneous factors 

such as marital status, employment level or prior criminal records. 

The tests for the additional direct effects will follow the 

models that test only for the direct effect of the treatment on the 

outcome of interest. The nonexperimental measures included the 

defendant age, ethnicity, employment level, prior arrests, and 

relationship status with the victim. All of these measures have 

in some fashion been shown in prior research as predictors of 

general offending patterns (Blumstein, Cohen, Roth & Visher, 1986; 

Gottfredson & Gottfredson, 1988), as well as violence between 

intimates (Fagan & Browne, 1994; Fagan, Garner & Maxwell, 1997; 

Hotaling and Sugarman, 1990). That is, it increases the chances of 

finding a treatment effect if one exists. In our analysis, we used 

a set of covariates which included defendant age, employment 

status, race, marital status, and prior arrests. 

.i 

Adding covariates to the analysis also allows us to specify 

two sets of interaction terms. These interactions will model how 

two measures of social control (marriage and employment) may 

mediate the direct effect of the treatment on intimate aggression. 

47 

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The choice of marriage and employment as the tested mediators is 

based upon a review of research in other areas of domestic violence 

interventions that had found these particular measures of social 

control as important factors in understanding how treatments may 

not necessary work equally for all batterers (see Sherman, Smith, 

Schmidt & Rogan, 1992; Pate & Hamilton, 1992). There are numerous 

ways of testing for the interaction of two independent measures on 

the 

interaction terms will be specified in such a way that they 

represented the product of two independent measures that were both 

coded as dummy (0 and 1) variables. The product or the new 

the outcome measures. Following Hardy (Hardy, 1993), .i 

interaction term also had the values of 0 or 1, with the suspects 

taking the value of 1 if they also had 1 on both of the other two 

measures, and 0 when they had a value of 0 for either or both of a the other two measures. 

Correcting for missing information Much if not all 

research in behavioral, economic, and social science is plagued 

with problems of missing information (Berk, 1983; Weisberg, 1985; 

Dubin & Rivers, 1989; Winship & Mare, 1992; Little & Schenker, 

1995; Breen, 1996). In general there are two types or causes of 

missing ingormation; item nonresponse and unit nonresponse (Little 

& Schenker, 1995). In the former type, missing information takes 

the form of unobserved or unmeasured information on one or more 

variables for a small subset of cases in a database. This sort of 

missing information can indicate systematic differences in 

subjects within the sample that if ignored can lead to a less 

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efficient estimate of an effect size or the complete withdrawal of 

certain cases from the sample in specific analyses (Weisberg, 1985; 

Little & Schenker, 1995). 

The second type of missing information occurs when cases 

included in a study represent nonrandom samples of a population. 

This type of missing data is often referred to as sample selection 

bias or unit nonresponse. Unlike the first type of missing data 

(item nonresponse) which is often due to researchers not recording 

certain responses, this type of missing data is typically created 

when subjects act in a manner that makes it impossible for the 

researchers to obtain responses from them for many if not all of 

the survey's questions (Dubin & Rivers, 1989). The nonrespondents' actions may include such things as not listing their 

telephone numbers, which would exclude them from studies that use 

telephone numbers as the means for sampling, or being unemployed, 

which would exclude them from studies that can only sample from 

those employed. A person's decision not to have a telephone listed 

or not to look for a job may represent a random process, but it 

could also be nonrandom. The nonrandom selection of cases from 

the entire population into a study is itself a social process and 

an aspect of social science that is often overlooked (Winship & 

Mare, 1992). For this project there were two opportunities for 

sample selection bias to occur, one opportunity was at the sixmonth victim interview and then again at the twelve month 

interview. Both of these selection opportunities will be 

independently addressed using separate selection models. 

.i 

49 

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The following analysis address& systematically both of the 

0 missing information problems. In the case of the missing 

information among some cases on the nonexperimental covariates, a 

two-step process suggested by Weisberg (1985) was followed to 

replace the missing data with valid information. The first step 

was to locate an alternative source of data for the measures with 

missing information and to use these alternative sources to replace 

the missing data in the primary database with valid information. 

After most of the missing data was replaced with valid data from 

an alternative source, we then moved onto the second step which was 

to use a statistical technique of imputing quasi-valid values for 

the remaining missing data. For this particular project we 

replaced the missing data using a multiple regression imputation 

procedure. This step specifically involved constructing a 

regression model that computed a predicted value for all cases 

based on those cases with valid data, and then uses this predicted 

value to replace the remaining missing data. 

In regards to the second problem of sample selection bias or 

missing victim interviews, a two step process proposed by Heckman 

(1979) was employed. The first step was to specify a model through 

the use of a multiple regression of the selection process that was 

captured in a single latent measure. This step required two 

different models, one for the six month interview and one for the 

into the original, substantive outcome models as independent 

measures (one for each interview period) to more fully specify the 

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structured relationship between the dependent and the 'set of 

0 independent measures. 

Treatment Attendance Rates 

We first compared differences in attendance rates between the 

8-week and 26-week groups. We expected that attendance would be 

better when treatment was compressed into a shorter span in the 8- 

week groups. 

The results, displayed in Table 5, were far more pronounced 

than we could have guessed. Roughly similar proportions of 

batterers began treatment in the 8-week and 26-week groups. 

Seventy-seven percent of those assigned to the 8-week groups 

attended at least one class compared to 71% of those assigned to 

the 26-week groups. But graduation rates were dramatically 

different. Sixty-seven percent of the men assigned to the 8-week 

groups graduated compared to just 27% of those assigned to the 26- 

week groups. We conclude that a much larger proportion of those 

assigned to treatment were exposed to the full treatment in the 8- 

0 

3 

week groups than in the 26-week groups. 

Criminal Justice Incidents 

Simple prevalence of new criminal incidents involving the same 

~- ~ 

' Chi-square (1)= 27.72, p < -001. 

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victim at six months and 12 months after assignment to treatment 

(i.e., date of sentencing) is presented in Table 6. At six months, 

reports to the police of new violence involving same victim and 

perpetrator differed significantly between treatment groups. Seven 

percent of the 26-week group failed at six months according to this 

measure compared to 15% of the 8-week group and 22% of the control 

group. A similar pattern is evident in Table 2 for criminal 

justice incidents 12 months after assignment. At 12 months, 10% .i of 

the 26-week group failed. The 8-week treatment and control groups 

are virtually indistinguishable, with failure rates of 25% and 26%, 

respectively. 

We now turn our attention to multivariate tests of criminal 

justice incidents. Multivariate models include Poisson regression 

models of the rate of offenses and Cox regression models of time to 

first new criminal justice incident. Both sets of models utilize 

all of the data captured in record searches which, for most cases, 

goes well beyond twelve months post-assignment. Record checks were 

done after the last sampled case had reached 12 months postassignment, so longer follow-up times were available for most 

cases. (With Cox regression, longer follow-up times increase 

statistical power.) 

Poisson regression of annual rate of criminal justice 

incidents Typically OLS regression is used when the quantity 

of a dependent measure of interest is specified rather than the 

quality or presence of some event. However, the application of OLS 

in the instances where the specified dependent variable is the 

52 

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count or a rate of some event is problematic (Gardner, Mulvey & 

Shaw, 1995). Overall, there are two reasons why OLS is 

inappropriate: (1) the OLS estimations can produce negative 

predicted values; and, (2) the hypothesis test used in OLS assumes 

certain properties of the variance of scores that are unlikely to 

be met with count data. To address these two problems, the Poisson 

and related regression models have over the last twenty years begun 

to replace the OLS regression as the primary means of analyzing 

dependent measures that are based on a counting process (Land, 

McCall & Nagin, 1996). 

The Poisson regression specifically models in a multivariate 

context the number of events during an interval of time. 

Generally, the observed distribution of the counts of events takes 

on a Poisson like curve, which is one where the number of cases per 

increasing count is less than the previous count. Because this 

sort of distribution is useful for handling infrequent events 

(e.g., instances where most cases have a value of zero or one), the 

Poisson regression has become invaluable to criminologists. Due to 

this property, our analysis used Poisson regression when addressing 

the question of whether the treatment reduced the quantity or rate 

of failures found in the officially recorded database of new 

domestic incidents reported to the authorities. 

a 

We adjusted the count of criminal justice incidents to an 

annualized rate to account for the unequal follow-up time across 

the suspects. This count includes all known recorded offenses that 

took place after the treatment assignment and makes no distinction 

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or adjustment for the severity or type of criminal offense. The 

first regression model (Model One; Table 7) provides the results 

from the classic experimental analysis: the mean of the dependent 

measure disaggregated by three treatment groups (control group, 

short treatment, and long treatment). This first regression shows 

that only the long treatment group had a significant reduction 

(40%) in the average number of new offenses when compared with the 

control group. The difference between the control group and short 

treatment group was not significant, but the direction of the 

treatment effect was also negative. Model Two then builds on Model 

One by adding additional control measures to account for the 

natural heterogeneity between and within the three experimental 

comparison groups. Again, the long treatment group shows a 

significant reduction in the number of offenses compared the 

control group. Beyond this one significant experiment-treatmenteffect, no other control measures show either a significant 

increase or decrease in the number of officially recorded offenses. 

This lack of a significant effect includes the measures of the 

suspect's age, ethnicity, employment status, and prior arrest, 

which have all been found in other research has significant 

predictors of recidivism among domestic violence batterers 

(Maxwell, 1998). However, beside the null effect for age, all of 

the effects from the other four control measures are in their 

expected direction. 

0 

.i 

0 

Models Three and Four add two sets of treatment by control 

interaction to the independent measures regressed in Model Two. 

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8 

a Poisson Regression of Annual Officially Recorded Offense a 

Model Model 2 Model 3 Model 3 1 

b s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(6) -~ 

Model Parameters 

An/ 

Short -0.24 0.30 0.8 -0.24 0.29 0.8 

Long -0.58 0.24 0.6 -0.57 0.24 0.6 * 

. Age 0.00 0.01 1.0 

Ethnicity(African-Ameilcan) 

Hispanic 

West I ndianlCa ri bbean 

Other Race 

Married 

Employed 

Prior Arrest 

-0.29 0.25 0.7 

-0.47 0.30 0.6 

-0.33 0.32 0.7 * 

0.19 0.20 1.2 

-0.24 0.21 0.8 

0.35 0.20 1.4 

I 

t ATV Employment 

Short ' Employment 

Long Employment 

ATV' Married 

Short' Married 

Long ' Married 

1 n t ere p t -1.10 0.13 -1.08 0.43 

-0.28 0.46 ' 

-0.30 0.34 

0.00 0.01 

-0.28 0.25 

-0.47 0.30 

-0.32 0.32 

0.22 0.20 

-0.12 0.26 

0.36 0.20 

0.07 0.58 

-0.52 0.49 

-1.17 0.44 

0.8 0.02 0.35 1.0 

0.7 -0.90 0.36 0.4 ' 

1 .o 0.00 0.01 1.0 

0.8 -0.28 0.25 0.8 

0.6 -0.45 0.30 0.6 

1.2 0.14 0.26 1.1 

0.9 -0.28 0.21 0.8 

1.4 (0.38 0.20 1.5 

0.7 -0.31 .0.32 0.7 

I .I 

0.6 

-0.65 0.60 0.5 

0.66 0.49 4.9 

" -1.03 0.43 

Model Fit -235.88 -234.52 - -236.52 

-244.89 -244.89 

20.75 

0.08 0.04 

-241.71 

Restricted Log likelihood -244.89 -244.89 Log likelihood 

Chi-square 6.36 

P-value 0.04 

16.74 18.02 

0.05 

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First, Model Three provides the results for the two treatment 

(short and long) by employment interaction terms. This model shows 

that neither of the two treatment groups were either more or less 

effective at reducing offenses among those employed versus those 

not employed. Finally, Model Four provides the results for the 

treatment by marital status interaction terms. This final 

regression model shows that those victims and suspect who were not 

married have likely accounted for the significant direct treatment 

effect, as the suspects in the not married but in the long 

treatment group were the only ones with a reduced number of 

officially recorded offenses. 

Time-to-first criminal justice incident To examine time from 

case assignment to first new incident reported to the police, we 

used Cox regression. The Cox regression model or the 

semiparametric proportional hazard model enables the efficient 

modeling of data in a multivariate context when the dependent 

measure is time censored (e.g., no case is followed for infinity). 

This analytical model has become an important tool for researchers 

evaluating criminal justice-based programs, since it can account 

for the uneven follow-up periods that are characteristics of 

therapeutic treatment or correctional intervention programs. In 

other words, this model can accurately analyze data collected on 

subjects over a time that is not equal in length nor 

indeterminable. 

0 

The Cox model specifically involves constructing a base-line 

hazard function for the event of interest (e.g., new arrest, new 

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drug use or any other discernable transition) that is dependant 

only those cases that are uncensored at a particular time-period. 

This hazard function is then defined as the probability of failing 

e 

during any particular time interval (e.g., a day), if the 

individual has survived to the start of that interval (Lee, 1992). 

The model can then introduce one or more prognostic variables 

which are used to estimate whether-the baseline hazard function is 

dependent on the level of each independent measure while jointly 

controlling for the effects of the other endogenous variables. In 

addition, time-covariant factors can likewise be introduced to test 

whether the baseline hazard function is dependent on a particular 

time interval or is proportional overtime. This report will 

capitalize on the Cox regression model when the analysis of the 

officially recorded data is concerned with the question of whether * treatment influenced the likelihood that aggression had occurred 

again by the suspects against the victims which were also known to 

the police. 

Table 8 provides the results from five regression models of 

the hazard or time-to-first new officially recorded offenses. 

Again, Model One provides the classic experimental analysis. This 

first model, similar to the one reported in Table 7, shows that the 

odds of a new offense were significant reduced among the long 

treatment group compared with the control group. In other words, 

at any particular time after the treatment assignment the 

likelihood of the first new offenses was reduced about 50 percent 

among those in the long treatment group when they were compared 

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with the control. Model Two also shows that this effect is likely 

not variant overtime as the two time-covariant by treatment 

interaction terms are not significant. Model Three then builds on 

Model One by adding the control measures used in the earlier 

regression model (Table 8; Model Two), and drops the timecovariance terms because they were not significant. Again, the 

direct negative effect of the long treatment remained significant. 

However, unlike the earlier regression model, two control measures 

are now significant and in their effects are in the expected 

direction. First, the "other" racial group had a significant 

reduced likelihood of failing when compared to the AfricanAmericans. Besides this significant effect, those with a prior 

arrest had a significant increased risk of failing at anytime 

@ 

during the follow-up period. 

The final two regression models reported in Table 8 provide 

the results from the same two sets of interaction terms that were 

reported on earlier in regards to the number of failures. Here the 

interactions are testing whether the hazard rates for the treatment 

comparison are dependent on whether the suspect and victim were 

married or whether the suspect was employed. Both of the 

regression models suggest that the direct negative effect of 

treatment is likely mediated by both the marital and employment 

status of the suspect. More specifically, those suspects assigned 

to the long treatment who were also not married or not employed had 

a longer average period of survival than those married or employed. 

In other words, marriage and employment increased the risk of 

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e8 

Cox Regression Model of Time-to- first Newdciall - y Recorded Offenses Against Same Victim 

Model Paramefers b s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(6) b s.e. Exp(B) 

ATV Short -0.21 0.29 0.8 -0.52 0.64 0.G -0.15 0.30 0.9 -0.16 0.47 0.9 0.108 0.36 1.1 

Long 

Model 1 Model 2 Model 3 Model 4 Model 5 

-0.72 0.26 0.5 '* -1.36 0.63 0.3 -0.74 0.26 0.5 " -0.75 0.39 0.5 ' -0.96 0.36 0.4 " 

ATV 

Short Time 

Long ' lime 

Age 

Ethnicity (African-American) 

Hispanic 

West India nlCa ri bbean 

a OtherRace 

Married 

Employed 

Prior Arrest 

ATV Employment 

Short Employment 

Long Employment 

Am' Married 

Short ' Married 

Long Married 

0.00 0.00 1.0 

0.00 0.00 1.0 

0.01 0.01 1.0 0.01 0.01 

-0.26 0.26 0.8 -0.26 0.26 

-0.50 0.31 0.G -0.50 0.31 

-0.76 0.39 0.5 '* -0.76 0.39 

-0.27 0.26 

0.09 0.22 1.1 0.09 0.22 

-0.28 0.22 0.8 

0.53 0.22 1.7 '* 0.53 0.22 

I .o 0.01 0.01 1.0 

0.8 -0.27 0.26 0.8 

0.6 -0.50 0.31 0.6 

0.5 ' -0.74 0.39 0.5 

I .I 0.05 0.26 1.0 

0.8 -0.32 0.22 0.7 

1.7 ' 0:55 0.22 1.7 ' 

0.01 0.60 1.0 

0.03 0.53 1.0 

8 

-0.65 0.62 0.5 

0.50 0.53 1.6 

8 1035.47 I 

1035.47 1035.47 Model Fit 

101 0.79 

1035.47 

101 0.80 24.40. 4, 24.80 7.903 

Log likelihood 

0.02 

Restricted Log likelihood 1027.1 I 

Chi-square 

P-value 

1008.15 . 1035.47 

1025.58 

7.90 9.1 5 0.01 

0.02 0.05 0.00 

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earlier failure among those assigned to the longer treatment group. 

Nevertheless, the overall effect for the long treatment group was 

still towards decreasing the risk (see Models 1 & 2), the effect 

was likely just not equal across all suspects. 

Incidents ReDorted bv Victims to Research Interviewers 

Simple prevalence of victim reports of violence to research 

interviewers is reported in Table 9. The table contains victim 

reports on surveys done approximately six and 12 months after 

assignment to treatment. In each survey, victims report on the 

immediately preceding two months. At six months, virtually no 

differences are apparent between groups. Twenty-three percent of 

the 26-week group reported a new incident compared to 19% of the 8- 

week group and 21% of the control group. Differences were larger 

at 12 months, following the same pattern as the criminal justice 

incidents, but still did not approach statistical significance. At 

12 months, 15% of victims whose cases were assigned to the 26-week 

group reported a new incident within the past two months compared 

to 18% of victims whose cases were assigned to the 8-week group and 

22% of victims whose cases were assigned to the control group. 

0 

Negative binomial regression There is one major 

limitation of the Poisson regression used above in analyzing 

treatment differences in new incidents reported to authorities. 

That is the assumption that the mean and the variance are identical 

and equal to the expected mean (Land, et al., 1996). When this 

assumption is not met the model is considered overdispersed, which 

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Table 9: Prevalence of incidents reported by vittims to research interviewers. 

*Chi-square (2)= 0.15, p=.926 

**Chi-square (2)=1.86, p=.394 

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can lead to incorrect estimations of variances and misleading 

inference about the effects of independent measures. To adjust for 

this problem an additional term that reflects the “unexplained 

between-subject difference is included in the regression model. 

(Gardner, et al., 1995, p. 393). This additional term in turn 

0 

changes the Poisson model into a negative binomial model, which 

only assumes that the dependent measure looks like a- Poisson 

Distribution, and not that all individuals have the same mean rate. 

Because the negative binomial model through the addition of one 

term removes the Poisson‘s assumption of equity, it provides 

.i 

greater flexibility for accurately representing the relative 

frequency of observed event count data (Land, et al., 1996). With 

the victim interview data on reports of violence, we performed a 

test which showed that ovedispersion was present. Therefore, we 

0 substituted a negative binomial for a Poisson model. 

Tables 10 and 11 provide the results from both the six and 

twelve month victim interviews. Here, the outcome measure, 

extracted from a modified CTS, is delineated as the maximum number 

of aggressive incidents by the suspect against the victim that she 

reported happening over the two months preceding the two 

interviews. The results show after correcting for sample selection 

bias and adding a term to address overdispersion, that neither the 

short nor the long term treatments seemed to have reduced 

significantly the frequency of aggression at about the six or 

twelve months periods. However, at both time periods and for both 

treatment groups the direction of the effect is negative (e.g., 

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T 10 

Nega!ive Binomial Regression of the Past Twanlh Frequerlq of Victimization @ Six Month Survey 0 i 

- 

Model Model 2 Model 3 Model 3 1 

Model Parameters b s.e. Exp(B) b. s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(B) 

An/ -1.53 1.34 0.2 -1.12 1.43 0.3 0.49 2.72 1.6 -2.93 2.16 0.1 Short 

Long -0.88 0.90 0.4 -1.02 0.91 0.4 -0.74 1.12 0.5 -1.05 1.28 0.3 

0.06 0.08 1.1 0.05 0.08 1.0 

Ethnicity (African-American) 

Hispanic 1.36 1.09 3.9 

West IndianlCaribkan 0.13 1.45 111 

0.66 1.96 1.9 

-1.74 1.45 0.2 

Other Race 

Married -0.44 1.02 0.6 0.23 1.312 1.3 -0.36 1.04 0.7 

1.24 1.12 3.5 

0.04 0.08 1.0 

1.38 1.11 4.0 1.68 1.25 5.4 

* 0.32 1.25 1.4 0.11 1.29 1.1 

0.96 1.84 2.6 1.04 1.96 2.8 

Age 

-1.39 1.24 0.2 -1.52 1.27 0.2 

Employed 

Prior Arrest 1.11 1.14 3.0 0.82 1.14 2.3 

AN Employment . 

Short Employment 

Long Employment 

-2.63 3.39 0.1 ' 

-0.68 1.73 0.5 

An/' Married 2.58 2.96 13.1 

Short ' Married 

Long Married -0.02 1.92 1.0 

-7.95 6.94 -10.75 8.94' -7.57 6.81 

6.45 9.07 8.15 8.38 7.48 8-18 .*a 

-4.79 7.63 

11.04 3.30 *" 9.0 2.46 *** 8.01 2.47 *** 8.72 2.40 10.34 10.31 Intercept 

Selection Bias ratio 

Scalar I 

-1 92.77 

-474.46 -473.1 3 -468.86 

Model Fit 

Log likelihood 

Restricted 694 561 .I 8 560.41 '.' 552.1 8 Log likelihood -545.7404 

C hi-qua re 

-1 99.21 77 -1 93.87 -1 92.77 

1 

P-value 0.00 0.00 - 0.00 0.00 . I 

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I Te 11 0 

Neqative Binomial Regression of the Past Two Month bequency of Victimization @? Twelve Month Surveya 

- Model 1 Model 2 Model 3 Model 3 

b s.e. Exp(B) I - 

Model Parameters b s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(B) 

AN Short -0.94 1.01 0.4 -0.79 1.18 0.5 -2.16 2.29 0.1 -2.10 1.66 0.1 

Long -i.29 0.81 0.3 -1.57 1.07 0.2 -1.70 1.47 0.2 -0.95 1.12 0.4 

Q.02 0.05 1.0 

I .o -0.85 1.06 0.4 -0.57 1.29 0.6 -0.51 1.21 0.6 

0.34 1.18 1.4 0.43 1.44 1.5 0.51 1.36 1.7 

0.10 1.69 1.1 0.00 1.85 1.0 -0.02 1.61 1.0 

-0.86 1.30 0.4 -0.98 1.28 0.4 -0.51 1.17 0.6 

-0.80 1.18 0.4 -1.18 1.41 0.3 -1.00 1.12 0.4 

-1.03 0.92 0.4 -0.83 0.96 0.4 -0.90 0.93 0.4 

I .o 

1 .o 

* 1.0 

1.90 2.47 6.7 

-3.52 2.82 0.0 

# 

I 0.01 0.05 1.0 0.01 0.05 1.0 

Age 

Ethniaty(African4merican) 

Hispanic 

West IndianICaribkan 

Other Race 

Married 

Employed 

Prior Arrest 

ATV ' Employment 2.06 2.90 7.8 1 .o 

0.20 2.11 1.2 

Short * Employment . 

Long Employment 

All/' Married 

Short Married 

Long Married - 

4.41 9.14 3.56 9.60' 5.49 9.21 

10.35 2.98 

-5.14 11.49 

1.62 7.93 

at. 

-1.02 10.12 -3.98 11.51 -2.27 12.12 4,. 

Intercept 

Selection Bias ratio 

Scalar 13.92 3.36 ++' 11.97 3.34 11.65 3.36 

Model Fit -1 87.30 -1 86.44 -1 82.28 

-529.49 

694.43 

0.00 

-1 91 -03 . 

-61 7.99 -551.84 -546.37b, Log likelihood 

Restricted Log likelihood 

853.92 71 9.85 729.09 Chi-square . 

P-value 0.00 0.00 0.00 

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reduction in the average frequency of aggression). In regards to 

the other nonexperimental factors tested, no other variable was a 

significant predictor of an increase or decrease in the level of 

aggression as well, and the two sets of interactions terms likewise 

indicated that the null direct effect of the treatments were not 

dependent on level of social control. In other words, the two sets 

of regression models reported in both tables are poor at explaining 

any variation of the frequency of intimate aggression beyond just 

the mean. 

5 

4 

Coanitive Chanae Measures 

Our measures of the cognitive change in batterers included 

conflict resolution skills, beliefs about domestic violence, and 

locus of control. Each of these scales has problems for use as a 

4 A set of identical logistic regressions model were also estimated 

using a dichotomized dependent measure for aggression instead of count of 

aggression. The results were similar'to the extent that no treatment groups 

were significant different from the controls. The only noteworthy differences 

between the two estimation procedures was that the logistic produced a 

significant positive effect of prior arrest on the odds of failing and the 

long treatment produced a nonsignificant increase in the odds of failing. 

Otherwise, the models were very similar 

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measure of cognitive change in batterers. The beliefs about 

domestic violence scale has limited reliability statistics. The 

conflict management strategies scale similarly has been littlestudied for test-retest reliability. The locus of control test has 

been problematic for use with batterers because of it assumes a 

fairly high level of cognitive functioning. (we sought to mitigate 

this problem by using a children's versiun of the scale.) 

Moreover, it could be argued that batterer intervention groups 

could teach participants how to answer items "correctly" on any of 

these scales without any true change in cognitive beliefs or 

behavior. Still, the group of scales used to assess cognitive 

change represented the most commonly-used indices at the time the 

study was conducted. 

.i 

The original analysis plan called for a repeated measures 

MANOVA test using the same set of covariates described above in the 

recidivism analyses. However, we were unable to carry out this 

0 

plan due to serious limitations in the data. First, the internal 

validity of the scales was low. The conflict resolution skills 

scale was respectable, averaging .71 over the six and twelve month 

interviews with batterers. Reliability of the locus of control 

scale averaged .69 over the six and 12 month interviews. The 

beliefs about domestic violence scale had lower reliability, 

averaging .57 over the two follow-up points. Second, ns for the 

three cognitive measures were very low. At the 6-month interview, 

we had 149 cases, and just 88 cases at the 12-month interview. 

Means and standard deviations for each of the three tests at 

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each of the two time points are bresented in Table 12. For each 

scale, means across the three treatment groups are remarkably 

similar, and none of the univariate F-ratios also presented in 

Table 12 come close to statistical significance. We have, 

therefore, no basis for claiming that treatment changed batterers' 

attitudes or ways of dealing with conflict. But again we note that 

limitations in the scales and in our data do not permit an adequate 

test of this hypothesis. 

a 

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Table 12: Means and Standards deviations for psychosocial outcomes* 

*Numbers on parentheses are standard deviations. 

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IV. CONCLUSIONS 

Our initial analyses showed that men assigned to a group 

treatment program for batterers were less likely to be the subject 

of future crime complaints involving the same parties than men 

assigned to an irrelevant treatment (community service). This 

difference was most pronounced at six months after group 

assignment, but held up over a full year. _. 

Subsequent analyses revealed interesting findings about length 

of treatment. Due to fortuitous circumstances, we wound up 

splitting our treatment sample into two subsamples distinguished by 

density of treatment sessions. All batterers randomly assigned to 

treatment were mandated to attend 39 hours of psycho educational 

group treatment based upon the Duluth model. However, some 

batterers received the 39 hours in 26 weekly sessions while others 

received it in longer biweekly sessions for 8 weeks. The former 

treatment model maximized time that batterers remained in treatment 

while the latter reduced the chances that batterers’ initial 

motivation would flag over time. 

a 

Our results showed that far more men successfully completed 

the 8-week group than the 26-week group. We expected, therefore, 

that men assigned to the 8-week group would have a lower rate of 

recidivism than men assigned to the 26-week group. However, only 

the 26-week group was statistically different from the control 

group on future crime complaints: The 8-week group and the control 

group were indistinguishable. Victim reports of violence to 

63 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

This document is a research report submitted to the U.S. Department of Justice. This report
research interviewers showed a similar pattern, but differences 

0 between treatment conditions did not approach statistical 

significance. 

Batterer intervention can be looked upon in one of two ways. 

It may be a learning process in which attitudes and behavior are 

modified in a relatively permanent way, Or it may be that batterer 

intervention simply suppresses violent behavior for the duration of 

treatment, but no permanent changes are effected. Our results do 

not support the model of treatment as a change process: If that 1 

were true, then the men in the 8-week group (who were finished with 

treatment long before the follow-up period was up) ought to have 

been as non-violent as their 26-week counterparts (who were in 

treatment for most of the follow-up period). Yet that is not what 

our results showed. Also, we did not find evidence that treatment 

altered attitudes toward spouse abuse, further suggesting that 

there was no basis for permanent changes. (However, the reader is 

again advised of serious limitations in the cognitive change scales 

and data.) 

Our results, then support the suppression model of batterer 

intervention. But they are only suggestive since the study was not 

designed to test the validity of various models of the treatment 

process. Moreover, they are at odds with other studies which have 

not tended to find a difference in recidivism according to length 

of treatment (Edelson and Syers, 1990; Gondolf, 1997a). Many 

current batterer programs are going to longer treatment models, but 

there is also substantial pressure from the defense bar and 

64 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

This document is a research report submitted to the U.S. Department of Justice. This report
economics to keep time in treatment to a minimum. Thus, the 

question of whether treatment works only as long as men attend 

groups is key to intelligent policy formulation. 

0 

How do our results fit into the literature on batterer 

treatment? If we concentrate only on the four quasi- and two true 

experiments (including ours), then we note that five of the six 

(Harrell, et. al. is the lone exception) reported results in the 

expected direction and all reported statistical significance on at 

least one outcome measure. i 

But even more striking are the effect sizes (i.e., strength of 

association between treatment and criminal outcomes) from these 

investigations. Effect size has been argued to be a more important 

index of treatment effects than statistical significance (e.g., 

Cohen, 1992; Rosenthal, 1991). It provides a measure of 

delectability of an effect which is independent of the baseline 

rate to which it is being compared (Bem and Honorton, 1994). (The 

power to detect the difference between .55 and -25 is different 

from the power to detect the difference between .50 and .20.) 

0 

We computed effect sizes for five of the six quasi- and true 

experiments. (Harrell's anomalous work was omitted from this 

analysis.) The effect sizes were computed on proportions of repeat 

violence culled from police records because it was the most 

commonly available measure from this group of studies. Effect size 

was assessed using Cohen's h (Cohen, 1988). In the five batterer 

treatment studies that found evidence in favor of treatment, effect 

sizes ranged from 0.108 to 0.946 (see Table 13). To place these 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

This document is a research report submitted to the U.S. Department of Justice. This report
effect sizes in context, consider the effect size of one of the 

early large clinical trials on the effect of aspirin on heart 

attack rates. In that research, more than 22,000 subjects were 

randomly assigned to take aspirin or a placebo. The study was 

stopped after six years because it was already clear that the 

aspirin treatment was effective (pe.00001) and today it is common 

medical practice for doctors to prescribe aspirin to prevent second 

heart attacks. Yet the effect size, as measured by Cohen's h, was 

only 0.068. Against this standard, the effect sizes seen in 

batterer treatment studies are quite substantial. 

A common technique in meta-analysis is to give studies quality 

ratings and then correlate the ratings with effect sizes. If the 

effect size decreases as quality of the research goes up, it is a 

good indication that the effect is not real (see, for example, 

Utts, 1991). This has often been the case in criminal justice. 

For example, early literature on pretrial diversion was generally 

0 

positive; but when a true experiment was conducted, no effect of 

diversion upon subsequent criminal behavior was found (Baker and 

Sadd, 1979). 

In contrast, the effects do not seem to disappear in the 

batterer treatment literature as the studies become more rigorous. 

Referring to Table 13, it is clear that treatment effects do not 

decline as we move from quasi-experiments to true experiments. The 

average effect sizes for the two true experiments (0.412) is 

virtually identical to the average for the quasi-experiments 

(0.416). 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

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Table 13: 

Effect Sizes 

Recidivism 

Treated Untreated 

Quasi-Experiments 

Dutton (1986) 4% 40% 

Chen et al. (1989) 5% 10% 

Dobash et al. (1996) 7% 10% 

Average 

. 

Ett'ect Site 

0.946 

0.193 

0.108 

j 0.416 

True-Experiments 

Palmer et al. (1992) 

Davis and Taylor (1 997) 

Average 

Recidivism 

Effect Size 

Treated Untreated 

10% 31% 0.537 

5 YO 13% 0.287 

0.4 12 

. .. 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

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Taken together, these studies provide a case for rejecting the 

null hypothesis that treatment has no effect on violent behavior 

toward spouses. However, the number of useful studies is small and 

more well-designed studies are warranted before coming to firm 

conclusions. 

Recommendations for Future Research 

The evaluations that have been done can provide useful 

information to future researchers. From these studies, we have 

estimates of treatment effect size which can be used to determine 

appropriate sample sizes for future investigations. Researchers 

will not need to guess whether they need 50 cases or 500 cases in 

order to attain the requisite statistical power needed to detect 

real effects. 

We recommend that several standards be applied to future 

investigations into whether treatment has an effect on violence. 

First, as recommended by Fagan (1996) and others, randomized 

experiments should be the design of choice. We recognize that 

random assignment when applied to judicial mandates to treatment 

are likely to prove difficult or impossible (since it is tantamount 

to sentencing by lottery and requires the agreement of prosecution, 

defense, and judiciary). However, true experimental designs are 

not unrealistic when applied to probationers who are mandated to 

treatment at the discretion of probation administrators. 

Jurisdictions in which treatment mandates are at the discretion of 

the probation agency are prime potential settings for research. 

67 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

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Our study provides a good illustration of the difficulties 

that can be encountered implementing a true experimental design. We 0 

had to make substantial concessions to court officials in order to 

gain their cooperation. Judges were allowed to override assignments 

to the control group in exceptional cases. This produced a high 

rate of judicial overrides of cases assigned to the control group. 

As we showed in the last chapter, the effect of including the 

override cases in the control group was to make the tests of 

treatment effects more conservative. (Yet, we still found'large 

treatment effects.) Also, we had to offer a treatment alternative 

that was more palatable to the defense than the lengthy and costly 

version that we started with. This proved to be a fortuitous 

change, however, since we found substantial differences in outcomes 

between men assigned to the 8-week and 26-week groups. We agree 

with the opinion of most serious researchers, however, that the 

benefits of random assignment outweigh the potential difficulties. 

10 

Second, measures and follow-up intervals need to be 

standardized so that results can be compared across studies. Too 

many studies have relied only upon batterer self-reports, known to 

vastly underestimate the true incidence of abuse (for an expanded 

discussion of this point, see Rosenfeld, 1992). The same kinds of 

measurement standards used in the National Institute of Justice's 

Spouse Abuse Replication Project (SARP) studies ought to be applied 

to batterer treatment: Investigations ought to include victim 

reports, crime complaints made to the police, and arrests. 

Batterers ought to be tracked at six-month intervals for at least 

68 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

This document is a research report submitted to the U.S. Department of Justice. This report
one year, and preferably two. Short-term measures are needed to 

assess immediate program effects -- effects that may be transient. 

Longer-term follow-up is needed to determine whether treatment 

leads to permanent changes. The use of both short-term and longterm measures is especially important in light of the suggestions 

from some of the SARP sites that law enforcement intervention may 

have deterrent effects in the short-run, but facilitating effects 

on battering in the long run (for a detailed discussion of 

measurement issues in the SARP data, see Garner, Fagan, and 

Maxwell, 1995). 

3) 

Third, investigations of the effects of batterer treatment 

need to be explicit in defining the standard against which 

treatment is being evaluated. Too many studies have compared men 

who go through batterer treatment to men who receive unspecified 

other sentences in the courts. To gauge the effects of treatment 

compared to the absence of treatment, it is imperative that 

batterers in the control group receive nothing relevant to reducing 

their propensity to batter. This may be possible when using a 

sample of probationers, some of whom are assigned to batterer 

treatment in addition to regular supervision and others of whom are 

assigned only to normal supervision regimes. 

0 

Fourth, researchers need to find ways to minimize attrition 

from treatment programs. Batterer program attrition typically runs 

greater than half of all participants assigned to treatment. This 

poses a serious dilemma for researchers, who must choose between 

analyzing groups as assigned (that is compare all individuals 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

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assigned to treatment to all individuals in the control condition) 

and comparing only program completers to controls. If treatment 

attrition is high, the first alternative results in overly 

conservative estimates of program effects since the treatment group 

is made up of many individuals exposed to minimal or no treatment. 

On the other hand, comparing only treatment completers to controls 

biases the analysis in favor of finding significant treatment 

effects since those who complete treatment are the "creamt1 of the 

0 

group of batterers assigned to treatment. 3 

Sherman (1992) argues that, assuming treatment attrition can 

be minimized, the clear preference is to "analyze as randomized". 

The critical question, according to Sherman, is whether the 

proportion of cases treated differently than the random assignment 

is larger than the proportion of cases with negative outcomes. On 

0 the hand, analyzing according to treatments as assigned becomes a 

problem when the treatment often fails to be delivered. A high 

rate of treatment "crossovers" reduces statistical power and 

increases the likelihood that an effective treatment will go 

undetected (Gartin, 1995; Weinstein and Levin, 1989). 

The best way out of this dilemma is to minimize treatment 

crossovers, most commonly attributable to treatment program 

attrition. Suggestions are that treatment attrition can be 

minimized by telescoping treatment into a short time span and by 

imposing penalties for failure to attend classes. Also, studying 

treatment programs located within corrections institutions -- where 

batterers have no choice about attending sessions -- would provide 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

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a way around the attrition problem. Such an institutional setting 

would provide a vehicle to examine the "dosage-response curve" 

indicating how treatment outcomes vary according to the number of 

sessions batterers are exposed to. (So-called "dosage-response 

curves" confound treatment effects with differences in participant 

motivation when they are based on the number of sessions batterers 

voluntarily attend.) This issue is important in light of the trend 

toward longer treatment programs yet -- excepting the present 

results -- unsubstantiated by empirical findings indicating3 that 

lengthy programs work better than shorter ones. 

* 

Fifth, researchers ought to make explicit issues which may 

restrict the extent to which their findings can be generalized. 

Particular attention needs to be given to the sample of batterers 

who participate in a research study. Are they court-mandated? Do 

they have extensive prior criminal histories or not? Do defendants 

have a chance to volunteer for treatment or are they sent to 

treatment regardless of their willingness to participate? Also 

potentially important is the criminal justice context within which 

treatment studies are set. Treatment program effectiveness may 

vary according to local court practices, linkages between agencies, 

sanctions for non-compliance, and so forth. 

Finally, researchers need to find ways to maximize interview 

response rates when interviewing victims about continuing abusive 

behavior from their spouses. It is common to have interview 

success rates below 50% when contacting victims six months or 

later. There are good reasons why rates are so low: Researchers 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

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are interviewing victims who did not initially agree to 

participate, they must rely on inaccurate contact information from 

the files of criminal justice agencies, and domestic violence 

victims and offenders are notoriously transient. Nonetheless, with 

interview success rates below SO%, it is difficult to make the case 

that interview data are representative of the sample as a whole. 

However, with sophisticated methods of follow-up .and judici.ous use 

of financial incentives, it should be possible to attain relatively 

respectable response rates (see Sullivan, Rumptz, Campbell;' Eby, 

and Davidson, 1996 for a discussion of minimizing survey attrition 

with battered women samples). 

@ 

There are parallels between the batterer treatment literature 

today and the literature on the rehabilitation of criminal 

offenders 15 or so years ago. In both literatures, the problem is 

not too few studies, but a paucity of sophisticated research. 

Calls that were made years ago by the National Academy of Sciences 

(Martin, Sechrest, and Redner, 1981) for agreement on outcome 

measures and randomized experiments in rehabilitation are just as 

relevant today for batterer treatment. The evolution in 

sophistication of batterer treatment studies is encouraging. 

Using randomized experiments and other designs that have a high 

degree of internal validity, we soon should be able to say whether 

batterer treatment works and to specify which program models are 

most effective. 

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of the author(s) and do not necessarily reflect the official position or policies of the

has not been published by the Department. Opinions or points of view expressed are those

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APPENDIX A 

ITEM FREQUENCIES ON ABUSE SCALE ADOPTED FROM HARRELL (1991) 

Item 

1. Forced sex 

2. Chokedstrangled 

3. Threatened to kill 

4. Beat up 

5. Threatened with weapon 

6. Used weapon 

7. Threw object e 

8. Pushedgrabbedshoved 

9. Slappedspanked 

10. Kickedhivpunched 

11. Hit 

Any of above 

6-Month 

Interview 

(n = 171) 

5% 

3% 

13% 

7% 

3% 

2% 

13% 

4% 

4% 

22% 

12-Month 

Interview 

(n = 189) 

4% 

3% 

7% 

4% 

2% 

1% 

5 Yo 

11% 

6% 

3% 

5% 

19% 

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APPENDIX B 

DIFFERENCES IN CASE CHARACTERISTICS PRIOR TO TREATMENT 

(8- AND 26-WEEK BATTERER TREATMENT GROUPS AND CONTROLS) 

8-week 26-week 

Group GrouD Controls p . 

(n=6 1) (nil 29) (n=186) 

3 

Has prior arrests? (YO yes) 43% 41% 37% .66 

Batterer employed? (% yes) 67% 63% 64% .84 

Batterer high school grad? (% yes) 64% 64% 61% .80 

Batterer African-American? (% yes) 36% 29% 41% .04 

Batterer age (years) 30.9 33.3 33.20 .17 

@ Battererhictim married? (% yes) 43% 42% 40% .89 

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APPENDIXC 

CHARACTERISTICS OF JUDICIAL OVERRIDES AND OTHER CONTROL CASES 

Overrides 

(n=52) 

DefendanVCase Characteristic$ 

Has prior arrests? (% yes) 40% 

Batterer employed? (% yes) 55% 

Batterer high school grad? (% yes) 57% 

Batterer African-American? (% yes) 35% 

0 Batterer age (years) 33.8 

Battererlvictim mamed? (% yes) 51% 

Other 

Controls 

(~134) 

36% 

68% 

63% 

42% 

33.0 

37% 

12-MonthRecidivism Outcomes 

Official reportdarrests (% yes) 2 1% 12% 

Victim reports to interviewers (% yes) 17% 25% 

e 

.65 

.10 

.80 

.77 

.58 

.09 

.14 (183) 

.37 (90) 

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Does Batterer Treatment Reduce Violence? 

A Randomized Experiment in Brooklyn 

EXECUTIVE SUMMARY 

Robert C. Davis 

Bruce G. Taylor 

Christopher D. Maxwell 

Victim Services Research 

346 Broadway, Suite 206 

NY, NY 10013 

January 2, 2000 

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ABSTRACT 

During the past two decades, pro-arrest laws have resulted in 

an increasing number of prosecutions of men who assault spouses or 

girlfriends. Researchers and practitioners have documented the 

difficulty of altering the behavior of convicted spouse abusers. As 

the courts have searched for effective sanctions for spouse abusers, 

they have increasingly come to rely on group treatment programs as 

the sentence of choice for the widening pool of men convicted of 

spousal assault. 

The greater reliance on batterer treatment programs makes it 

important that we can document that such programs effectively reduce 

the propensity of offenders to commit new violence. There is no 

shortage of evaluations of batterer treatment programs: Some three 

dozen have appeared in the literature since the 1980s. Most of 

these studies have methodological deficiencies, which make it 

difficult to interpret their findings. But evaluation studies have 

become more sophisticated as time has passed. 

The present study represents one of the first attempts to 

conduct a test of batterer treatment using a true experimental 

design. The design randomly assigned 376 court-mandated batterers 

to batterer treatment or to a treatment irrelevant to the battering 

problem (community service). All men assigned to batterer treatment 

were mandated to 39 hours of class time. But some were assigned to 

complete the treatment in 26 weeks and others in eight weeks. Men 

assigned to the control condition were sentenced to forty hours of 

community service. For all cases in the study, interviews were 

attempted with victims and batterers at 6 months and 12 months after 

the sentence date. In addition, records of criminal justice 

agencies were checked to determine if new crime reports or arrests 

had occurred involving the same defendant and victim. 

The results showed that treatment completion rates were higher 

for the eight-week group than for the 26-week group. However, only 

defendants assigned to the 26-week group showed significantly lower 

recidivism at 6 and 12 months post-sentencing compared to defendants 

assigned to the control condition. The groups did not differ 

significantly at either 6 or 12 months in terms of new incidents 

reported by victims to research interviewers. We interpret the 

results to indicate that batterer intervention has a significant 

effect on suppressing violent behavior while batterers are under 

court control, but may not produce 

' 

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INTRODUCTION 

Over the past two decades, the law enforcement response to 

domestic violence has become increasingly tough. Pro-arrest police 

policies have been promoted by advocates and widely adopted by 

police departments across the country (Buzawa and Buzawa, 1996). 

Increasingly, prosecutors as well have removed discretion 

traditionally given victims of domestic violence and insisted that 

cases be pursued to conviction regardless of victim desiws or 

willingness to cooperate (Rebovich, 1996; Hanna, 1996). These 

changes have meant that criminal courts have had to sanction an 

expanding pool of batterers, and they have increasingly come to 

rely upon group treatment programs as the sanction of choice. 

There are compelling reasons why group-treatment programs for 

batterers have become a popular mode of court sanction. Even in 

serious battering cases, many victims choose to stay with abusive 

partners. Such victims are interested in sanctions which offer 

them safety from violence, not retribution or punishment that will 

jeopardize their partner’s ability to earn a living. Alternative 

sanctions commonly used in other crimes have little face validity 

in abuse cases: There is little reason to believe that fines, 

community service or probation without special conditions will stop 

batterers from abusing their spouses. 

0 

There is no shortage of evaluations of batterer treatment 

programs. But the vast majority has serious methodological flaws 

which make it impossible to distinguish between treatment effects, 

temporal effects, and selection effects. Generally, the evaluation 

a 

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2 

literature shows an evolution toward more rigorous science since 

0 the first batterer treatment studies appeared in the literature in 

the early 1980s. The study we describe represents one of the first 

attempts to conduct a test of batterer treatment using a true 

experimental design which randomly assigns court-mandated batterers 

to batterer treatment or to a control condition. 

The Nature of Batterer Treatment 3 

The first group programs for batterers were begun during the 

late 1970s. Feminists, victim advocates, and others realized that 

providing services to victims of abuse and then returning them to 

the same home environment did little to solve abuse problems 

(Healey, Smith, and O’Sullivan, 1997). Group treatment was 

believed to be more appropriate than individual counseling or 

marital therapy because it expanded the social networks of 

batterers to include peers who are supportive of being nonabusive 

(Crowell and Burgess, 1996). Groups also proved to be less 

expensive than one-on-one counseling sessions. The earliest 

batterer groups were educational groups which sought to promote an 

anti-sexist message (Gondolf, 1995) . With the passage of time, 

they gradually incorporated cognitive/behavioral therapeutic 

techniques and skill-building exercises. 

As states introduced pro-arrest statutes during the 1980s the 

number of batterers arrested and convicted increased, and group 

treatment became the treatment of choice for the courts. Courtmandated batterer treatment significantly increased and diversified 

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3 

the number of batterer programs nationally (Feazell, Mayers, & 

0 Deschner, 1984). A recent estimate places the proportion of court 

mandates in treatment programs at 80% (Healey, et. al. 1997). 

Batterer treatment may be required by criminal courts as part 

of a pre-trial diversion program, may be ordered by judges as part 

of a sentence, or may be imposed by probation agencies empowered to 

set special conditions of probation (Hamberger & Hastings, 1993). 

In at least one major urban jurisdiction, the district attorney 

sometimes agrees not to file charges at all if a brief treatment 3 

program is completed (Davis and Smith, 1997). In some states (see 

Ganley, 19871, civil courts as well as criminal may mandate a 

batterer to treatment (e.g., as a condition related to child 

visitation). 

Many batterer programs are run by probation departments, while 

0 others are run by mental health practitioners, family service 

organizations, or victim service programs. Intake practices vary, 

with some programs accepting all court referrals and others 

exercising discretion in excluding persons with prior convictions 

or substance abuse problems. Supervision of batterers in treatment 

can most often falls to probation officers, but is sometimes 

undertaken by others - and increasingly by judges. Historically, 

supervision has been lax, drop out rates high, and sanctions 

unevenly applied. Recently, however, supervision has become 

stricter and sanctions for failure to attend sessions more common. 

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The Evaluation Literature 

Over the last two decades there have been many empirical 

studies on batterer treatment programs. There are at least six 

published reviews of over 35 published single-site evaluations 

(e.g., Eisikovits & Edleson, 1989; Gondolf, 1991,1995; Rosenfield, 

1992; Saunders, 1996a; Tolman & Bennett, 1990) and eight research 

0 

reviews (e.g., Davis and Taylor, in press; Hamberger & Hastkngs, 

1993; Crowell & Burgess, 1996; Dobash, Dobash, Cavanagh & Lewis, 

1995; Dutton, 1988, 1995; Rosenbaum & O'Leary, 1986; Saunders & 

Azar, 1989; Tolman & Edleson, 1995). 

However, the volume of the literature is deceptive. In fact, 

there have been only a handful of investigations that can make any 

legitimate claims about differences between treated batterers and 

untreated batterers. The batterer treatment literature has gone 

0 through three generations of studies. Most recent have been 

investigations which have randomly assigned batterers to treatment 

conditions. These are the strongest designs. Quasi-experiments of 

varying quality appeared somewhat earlier in the literature. The 

oldest, and by far the largest, portion of the empirical literature 

consists of studies which examine only batterers assigned to 

treatment programs. Included in this set of studies are: (a) 

studies which assess violence or other individual outcomes only 

after batterer treatment, (b) studies which measure violence before 

and after treatment, and 0 studies which compare violence of 

batterers who complete treatment with batterers assigned to 

treatment, but do not attend. Although the methodologies of early 

4 

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studies do not tend to be strong, they are important because they 

@ laid the foundation upon which stronger designs could be developed. 

Studies Without a Comparison Group 

Non-experimental one group post-test only designs 

At least 15 published studies have used designs which generate a 

single measure of treatment effectiveness: violence following 

completion of treatment (see Table 1). Ten measured recidivism 

based only upon batterer self-reports. Only four of the fifteen 

3 

studies had substantial sample sizes (which we have arbitrarily 

defined as greater than 100) or lengthy follow-up periods (which we 

have defined as one year or greater). 

Recidivism rates in this group of studies vary widely, from 7% 

to 47% (mean 26%). Interpretation of results is difficult at best 

0 without a comparison group or pre-test information with which to 

compare outcome measures. 

Non-experimental one group pre-test and post-test designs 

At least seven published studies compared violence among 

treated batterers after program participation to violence levels 

prior to participation (see Table 2). Three of the seven studies 

included both victim and batterer self-reports, but just two had 

follow-up periods of at least a year and none of the studies 

examined police records. Two of the seven studies had sample sizes 

greater than 100. Of the six studies that reported treatment 

attrition rates, four of the studies had attrition rates of 25% or 

less. 

5 

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Table I : Batterer Treatment Evaluations Using, a Post-Test Only Design . 

Beninati (1989) 16 

Johnson and Kder 

( 1990) 687 

:.. . ,::.:. ::.::i: .. ::.,;;;;:,.;; :... 

ttn t&~ . ... .,.. :. 

:.;.;::..:.: :.:::.: ::: ._..... ::.:...:. -.:.:.:.:.:.:.:.: 

'urdy & Nickle (I98 I) I70 I Batterer 6 months 41% Unknown 

I 

Batterer 50% I l2 

Deschner (1984 8 months 15% 

I 

I I 90 

Feazel, Mayers. and 

Deschner (1984) 25% Unknown 

0% 

Batterer 

I 

Batterer Ig fdleson, Miller, Stone. 

and Chapman (1985) 7 to 2 I weeks 22% 

3 

Unknown 

~ I 

Unknown Baltcrer I Ncidig. Friedman, and 

Collins (1985) 4 months 13% 

-~ 

Battercr 2 months to 3 years 27% Unknown 

20 months 

3 months 

3 months to a few yews 

6 months 

9 months 

Unknown 

1 year 

5 months 

Hmis (I 986) 40 

53 35% Debtaris and Jackson 

( 1987) Batterer 83% 

~ 

19% (Victim) 15% (Police) 

-~ I 67 

Long, Coates. and 

Hoskins (1987) Victim, Police 76% 

14s Shupe, Stacey & 

Hazlewood (1987) 

Tolman, Beeman, and 

Mendoza (1987 48 

Victim, Batterer 30% (Victim) 18% (Batterer) 3 1% 

Victim 47% 68% 

-~ 

86 zdleson and Grusmski 

(1988) (Study 2) Victim 33% 0% 

Batteret 19% 25% 

~~ 

106 Hambergcr and 

Hastings (1990) Batterer 3 0% 16% 

Battercr 7% 3 0% 

42% I 99 

Tolmsn and Bhosley 

(1991) 

50% 

- 

1 year I Victim 

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. Table 2: One Group Pre and Post-Test Design 

. . . . . . . 

Batterer Lk 

Victim 

Batterer 

Batterer 

Pre-Test 13.4 All DV acts (Batterer reports) / 

Post-Test 4.6 All DV acts (Batterer reports) 1 

Pre-Test 2 I .3 All DV acts (Victim reports)/ 1 

Jost-Test 6.1 All DV acts(Victim reports) (For 

all differences, P<.05) 

Dutton (1986) 

Part 1 

i months to 

3 years 

10% 

18% 

nknowi 

100% (Pre-treatment) 

9% (4 months) 

27% (6 Months) 

(P< .05) 

3 Rosenbaum 

(1 986) 

4&6 

Months 11 

Pre-Test 5.1 DV acts / Post-Test 0.29 DV acts 

(P .Os) Waldo (1 986) 23 6 Months 

14 months 

1 year 

Pre-Test 39% / Post Test 30% 

(Statistical significance not reported) Shepard (1987) 92 25% 

35 

Batterer 

3atterer, Victim 

(Combined 

measure) 

Hamberger and 

Hastings (1 988) 

Part 1 

Pre-Test 20.9 DV acts / Post-Test 5.3 DV acts 

(P < .001) 0% 

- 

53% Meredith & 

Bums (1990) 

Physical, verbal & emotional abuse all reduce( 

at post-test (% not reported) 125 Batterer, Victir 3 months 

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All seven studies reported lower recidivism rates following 

treatment (but results of one study were not statistically 

significant; two studies did not report probability statistics). 

However, with this type of design, reductions in recidivism 

cannot be attributed necessarily to the effects of treatment. This 

is true because studies have repeatedly shown that domestic 

violence declines after the police are called, even if nothing else 

is done. In fact, research suggests that only about a third of 

batterers commit repeat domestic violence within the next six 3 

months after the police intervene (see, for example, Davis and 

Taylor, 1997; Sherman, 1992; Fagan, Friedman, Wexler, and Lewis 

1984). The post-treatment violence rates displayed in Table 2 also 

average about one-third -- in other words not different than one 

might expect even if the batterers had not undergone treatment. 

Comparing treatment drop-outs versus completers Six studies 

compared outcomes between batterers who completed treatment and 

batterers assigned to a treatment program, but who failed to 

complete treatment (see Table 3). Four of the six studies had 

sample sizes under 100. Only two of the six studies had follow-up 

periods of at least one year, and just one included more than a 

single measure of recidivism. 

The most serious flaw in these six studies is that the treated 

and untreated (dropout) groups are almost certainly not comparable 

in complex ways prior to treatment. As pointed out by Palmer, 

Brown, and Barrera (19921, attendance is a confounding factor 

because better attendance is likely an indication of higher 

6 

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Halpern (1 984) 

Table 3: Quasi-Experiment (Dropouts Vkrsus Completers) 

Hawkins & Beauvais 

(1985) 

Douglas & Perrin 

(I 987) 

Edleson and 

Grusmski 

(1988, Studyl) 

Edleson and 

Grusmski 

( 1988, Study 3) 

Hamberger and 

Hastings 

(I 988) 

Part 2 

84 

106 

40 

86 

159 

71 

Victim 

Police 

Police 

Victim 

Victim 

Batterer, 

Jictim, Polic' 

(Combined 

measure) 

3 months 

6 months 

- 

6 months 

lbout 5 tc 

9 months 

1 year 

- 

1 year 

18% dropouts I 15% completers (N.S.) 

18% Dropouts / 18% completers (N.S.) 

5 

29% Dropouts I 15% Completers 

(No Statistics Reported) 

46% Dropouts /32% completeres (P < .03) 

48% Dropouts / 41% completers (N.S.) 

47% dropouts / 28% completers (P c.06) 

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motivation to change, even before treatment. Therefore, 

differential recidivism between program completers and drop-outs 

could be due to motivational differences in the two groups that 

existed prior to treatment. Surprisingly, however, only one of the 

six studies reported significantly lower recidivism rates for the 

completers (four of the other five studies were in the predicted 

direction but either had results that were not statistically 

significant or did not include inferential statistics). 

0 

3 

The best use of this group of studies is to describe the 

characteristics of people that drop-out of treatment -- information 

potentially useful to program developers to improve batterer 

groups. Results have indicated that those who do not complete 

treatment are more likely to be victims of child abuse (Grusznki & 

Carrillo, 19881, unemployed (Hamberger & Hastings, 1988; ), 

uneducated (Grusznki & Carrillo, 1988), young (Haherger & 

Hastings, 19931, psychologically disturbed (Hamberger & Hastings, 

1989; Grusznki & Carrillo, 1988), and substance abusers (Hamberger 

& Hastings, 1990). 

Quasi-Experimental Non-Equivalent Matched Groups 

We found four studies in which batterers mandated to treatment 

by the courts were compared to batterers who received other 

interventions. This group of studies is the first we have examined 

which addressed in a rigorous fashion the issue of whether 

treatment works. There is a notable difference in design details 

between these four quasi-experiments and the other studies reviewed 

7 

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Dutton (1986) 

Part 2 

Chen, Bersani, 

Myers, and 

Denton (1989) 

Harrell (1 99 1) 

Dobash et a1 

(1 996) 

Table 4: Quasi-Experiment (Matched Control Group) 

. . . . . . . . 

100 

22 1 

348 

3 13 

Police 

Police 

Battered 

Victim 

[Combinec 

measure), 

Police 

victim & 

court 

reports 

5 months to 3 

years 

9verage of 14 

months 

6 months for 

batterer & 

victims, 15 

and 29 

Months for 

police 

3& 12 

months 

40% No treatment / 4% Treatment (P < .001) 

10% (0.53 DV acts) No Treatment I 

5% (0.35 DV acts) Treatment (P < .Os) 

Peps Attended >75% TX less recidivisim than controls(P<.05) 

IS% severe violence No Treatment IZO%Trubncnt (P=N.S.), 

IZ%physiuI qgression NoTX/43%Treatment (Pc.01) 

736 New DV ChorgLs No Treatment I 19% Treatment (P < .OS) 

7% treated, 10% untreated (court reports 12 months) 

30% treated, 62% Untreated (victim 3 months) 

33% treated, 75% untreated (victim 12 months) 

No probability statistics provided 

0% 

Unknown 

24% 

Unknow 

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thus far. All four of the studies had smple sizes greater than 

100 (see Table 4). None of the studies relied solely on batterer 

@!!elf-reports. All four had follow-up periods of at least one year. 

The first quasi-experiment was reported by Dutton (1986). His 

sample consisted of 100 convicted batterers on probation. He 

compared 50 batterers who were treated within a cognitivebehavioral group model to 50 batterers who were not designated to 

receive treatment. The treatment group had a 4% recidivism rate 

compared to 40% for the control group based upon police reports. 

However, although Dutton reports that groups did not differ on 

several demographic measures, pre-treatment comparability of the 

groups is highly suspect: The control group was composed of 

batterers whom probation officers did not select for treatment, 

some of whom were explicitly rejected by therapists as unsuitable 

for treatment. The treatment group consisted of only batterers who 

completed the treatment program. Dutton does not report what 

proportion of all batterers assigned to treatment dropped out but, 

based on other work, we have to assume that it was a large 

proportion. 

P 

0 

Chen et al. (1989) conducted a quasi-experiment involving 120 

batterers assigned to treatment by the courts and 101 comparison 

batterers drawn from court calendars who were not mandated to go to 

treatment. (No details are given on how the controls were selected 

or what the outcomes were of their court cases, although the 

authors state that the samples proved to be well-matched 

demographically. 1 . Sixty-three percent of the men assigned to 

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Harrell's analysis included only batterers in the treatment 

group who actually completed treatment. Comparisons of recidivism 

were based on a combined measure of the victim and perpetrator 

reports of violence six months after case disposition. In 

addition, police records were reviewed 15-29 months after case 

disposition. Surprisingly, a significantly larger percentage of 

those in the treatment group committed new violence than those in 

the control group for two of three measures that she repsrts. 

(The third measure is in the same direction, but not statistically 

significant.). For example, 7% of the control group and 19% of the 

treatment group were charged with new domestic crimes. While 

Harrell's study may be limited in its ability to distinguish 

between selection effects and treatment effects, it certainly adds 

controversy to the debate about the efficacy of treatment programs. 

Recently, Dobash, Emerson-Dobash, Cavanagh and Lewis (1996) 

reported on a quasi-experiment evaluating a treatment program in 

Great Britain. Dobash et al. examined 256 domestic violence cases 

from sheriffs' courts in Scotland in which defendants were 

sentenced to batterer treatment or to another sentence (probation, 

court supervision, or prison). Few details are given about how the 

control group was selected, but the authors note that batterers in 

the treatment group were significantly older and more likely to be 

employed than batterers in the control group. (These differences 

are reminiscent of pre-treatment differences in Harrell's study.) 

It is not specified whether Dobash, et. al. included in their 

analyses all batterers assigned to treatment, or only those who 

10 

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completed treatment. According to court reports at 12 months 

follow-up, 7% of the treatment group recidivated compared to 10% of 

the control group: No statistical tests were reported to indicate 

whether the difference was significant. Data from victim surveys 

indicated that half as many batterers assigned to treatment 

committed new violence at three or 12 months as controls. (These 

two comparisons are reported to be statistically significant, 

although no specific information is provided.) However, the 

success rate for interviews was low: Dobash et al. interviewed only 

43% of the victims at the first follow-up interview, 34% at the 

second interview, and 25% at the third interview. 

Randomized Experiments 

m 

B 

As pointed out by Palmer et al. (1992), quasi-experiments on 

batterer treatment cannot be relied upon to produce unbiased 

estimates of the effects of treatment. This is true because we 

cannot know whether batterers assigned to treatment and controls 

are equivalent prior to application of the treatment. In some 

quasi-experiments (such as the Dutton, 1986 or Harrell, 1991 

studies), we know for certain that selection bias favored finding 

treatment effects (because the control group was comprised of 

batterers more prone to recidivate than those in the treated 

group). 

It can be argued that initial differences between groups can 

be controlled statistically, but this is only true if all relevant 

initial differences are known to researchers. For example, a 

researcher may discover pre-treatment differences in employment, 

11 

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marital status, and criminal history between those assigned to 

batterer treatment and controls, and these differences may be 

statistically controlled in analyses. However, groups may well 

have differed on less tangible and more fundamental factors such as 

emotional maturity as well. If such factors are not controlled 

(because they are not known) and they are correlated with outcome 

measures, then the results of the study are uninterpretable. The 

safest way to ensure that estimates of sample means are unbiaged is 

through random assignment of batterers to treatments. 

Palmer et. al. conducted the first experiment with random 

assignment to a true no treatment control group. The number of 

subjects in the experiment was far smaller than one would expect to 

need to detect treatment effects: Fifty-nine probationers were 

assigned using a "block random" procedure to either a ten-session 

psychoeducational group (combining group discussion with 

information) or a no treatment control group: Participants were 

assigned to treatment if a new group was to commence within three 

weeks; otherwise they became part of the control group. In only 

two cases was a defendant assigned to the control condition 

reassigned by court officials to the treatment condition. 

Attrition was kept within a respectable range: 70% of the men 

assigned to treatment attended at least seven of the required 10 

sessions. 

It is significant that this is one of the only studies to 

compare all batterers assigned to treatment (not just those who 

completed treatment) with controls. Palmer and her colleagues 

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examined police reports six months post-treatment and found 

recidivism rates (domestic physical abuse or serious threats) for 

the treatment group to be just one-third that of the control group 

(10% compared to 31%). Even with the small N, this difference was 

. statistically significant. While Palmer et. al. attempted to 

generate additional violence measures from surveys of interviews 

and batterers, low response rates combined with a small N precluded 

any analysis of recidivism based upon interview data. 

a 

3 

Two additional randomized experiments are in progress. 

Dunford (1997) is in the final stages of comparing treatment 

outcomes for 861 legally married Navy couples in which physical 

abuse had come to the attention of Navy authorities. These cases 

were randomly assigned to one of four treatments, including (a) 26- 

week batterer treatment (based on a cognitive/.behavioral model), 

0 (b) 26 weeks of couples counseling, 0 rigorous monitoring 

(including monthly calls to victims and semi-annual police record 

checks), and (d) establishing a safety plan for victims. The 

safety planning was intended by the investigators as a no-treatment 

control against which to compare the effects of the other three 

treatments. (Safety planning was given to victims in each of the 

other three conditions as well.) This would seem to be a fairly 

good no-treatment condition, in so far as the men in this condition 

received no intervention. Victims and batterers are being 

interviewed every six months over a period of two years. Feder 

(1996) has assigned batterers placed on probation to either a 26- 

week educational batterer program based on the Duluth model or a 

13 

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not mandated to treatment. Multiple measures of 

.1 be assessed (victim, batterer, police records, 

probation records) for six months and one year. 

PurDoses of the Present Study 

We sought to add to the incipient literature on randomized 

studies of batterer treatment. Although any form of design can be 

criticized, we concur with Fagan (1996) that randomized experiments 

entail less serious problems than other designs. A properly 

3 

executed randomization process is the only way to ensure that 

treatment effects are not confounded with pre-existing subject 

characteristics. Our study adds to the literature on randomized 

experiments in several important ways. 

Unlike the sites of the Palmer and Feder experiments, 

batterers in the site of our study were mandated to treatment by 

judicial order (in the sites of the other two studies, orders to 

treatment were made by probation departments). This difference has 

implications for the kinds of batterers studied. The Palmer and 

Feder studies had a wide sampling frame, including all or most 

batterers sentenced to probation, regardless of the batterers' 

willingness or unwillingness to enter into treatment. In our 

study, batterers were only eligible for inclusion if all parties to 

the case (prosecution, defense, and judge) agreed that treatment 

was appropriate. Such agreement was forthcoming in a small 

percentage of cases, most often because the defense refused to 

agree to treatment. Thus, our results are less easy to generalize 

14 

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The Palmer experiment found a significant effect of treatment 

although the sample size was surprisingly small because the 

treatment effect size was extraordinarily large. Our work planned 

sample size based upon an examination of effect sizes described in 

the literature. Thus, the design contains sufficient power into to 

provide for adequate tests of the effects of treatment upon several 

indicators of violence and attitudes. 

0 

Due to fortuitous circumstances, we wound up splitting our 

treatment sample into two subsamples distinguished by density of 

treatment sessions. (Readers interested in detail on the events 

that led to the change in treatment length are referred to the full 

report.) All batterers randomly assigned to treatment were 

mandated to attend 39 hours of psycho educational group treatment 

based upon the Duluth model. However, some batterers received the 

39 hours in 26 weekly sessions while others received it in longer 

biweekly sessions for 8 weeks. The former treatment model 

maximized time that batterers remained in treatment while the 

latter reduced the chances that batterers' initial motivation would 

flag over time. 

3 

0 

Finally, our work included both short-term (6-month postsentencing) and intermediate-term (12-month post-sentencing) 

follow-up on treatment outcomes. Short-term outcomes are important 

to assess because any effects of treatment may be short-lasting. 

We know that the likelihood of violence declines as time passes 

from the time a domestic complaint is made to the police (see, for 

example, Davis and Taylor, 1997). Any early differences in 

16 

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violence due to treatment might therefore disappear as violence in 

the control group came down over time. Longer term follow-up is 

also important to determine whether any short-term effects of 

0 

treatment hold up in the months after batterers are no longer 

attending treatment and under court control. 

17 

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METHOD 

Overview 

The study was conducted using a true experimental design in 

which 376 criminal court defendants were mandated to attend a 40- 

hour batterer treatment program or to complete 40 hours of 

community service. The random assignment was -made at Sentencing, 

after all parties (judge, prosecutor, and defense) had agreed to 

batterer treatment, if it was available based on the tandom 

assignment process. 

Batterers and victims were interviewed about new violence on 

three occasions: At the time of sentencing, six months after 

sentencing, and twelve months after sentencing. Official data on 

new complaints to the police and new arrests were gathered six and 

0 twelve months after sentencing. 

Cases Included in the Studv 

The sampling frame consisted of spousal assault cases in Kings 

County (New York) Criminal Court in which all parties had agreed in 

principal to accept batterer treatment, if the defendant was 

accepted by the Alternatives to Violence (ATV) program. This 

proved to be a small percentage of cases adjudicated within the 

course of intake. Intake began on 2/19/95 and ran through 3/1/96. 

During that time, 376 cases were taken into the sample. 

In nearly two-thirds (64%) of the cases in the study, 

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defendants were charged with 3rd degree assault (a class A 

0 misdemeanor). An additional 19% were charged with felonious 

assault (although pleas would be to misdemeanor charges). The 

remaining 17% were charged with violating restraining orders, 

menacing, harassment, and other charges. Court dispositions on 

cases in the sample were most commonly guilty pleas followed by a 

conditional discharge Twenty-three percent of the cases were 

adjourned in contemplation of dismissal (a form of pretrial 

diversion in which cases are dismissed and records expunged if 

3 

defendants avoid arrest and adhere to judicial conditions for six 

months). Conditional discharges and probation place defendants 

under court control for a period of one year, compared to a period 

of six months for most adjournments in contemplation of dismissal. 

Treatments 

Batterer treatment The batterer treatment program was Victim 

Services' Alternatives to Violence (ATV), based upon the Duluth 

model. The original model mandated 26 weeks of attendance at a 

weekly group meeting that lasted one hour. The course was rooted 

in a feminist perspective and assumed that domestic violence is a 

by-product of male and female sex roles which result in an 

imbalance of power. The curriculum included: Defining domestic 

violence, understanding the historical and cultural aspects of 

domestic abuse, and reviewing criminal/legal issues. Through a 

combination of instruction and discussion, participants were 

encouraged to take responsibility for their anger, actions, and 

19 

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reactions. Sessions were conducted in either English and Spanish 

by two leaders, one male and one female. 

ATV had changed its format just at the time that the 

experiment began, expanding the number of required hours from 1-1/2 

hours once a week for 12 weeks to 1-1/2 hours once a week for 26 

weeks. The change was made to conform with New York State 

guidelines and was in line with national trends. However, the 

lengthened program became a sore spot for Legal Aid Society 

attorneys who defend the vast majority of defendants in Brooklyn 

Criminal Court judged to be indigent. While Legal, Aid 

administrators had pledged cooperation (and, indeed, made good on 

that pledge), staff attorneys began to advise their clients against 

involvement in the new version of the ATV program. Intake slowed 

to the point that we would have been unable to complete intake 

within any reasonable time frame. At a meeting with Legal Aid 

staff attorneys we realized that their objections to ATV stemmed 

from the increased time that their clients were under court control 

and from the increased session fees that their clients paid over 

the course of 26 sessions. 

It became clear that, if we were to complete intake, we would 

have to accommodate the Legal Aid attorneys' objections to the 26- 

week batterer treatment program. Therefore, with the help of ATV 

administrators, we designed a new 8-week format through which 

participants could complete the same 40 hours of group time through 

bi-weekly 2-1/2 hour sessions with lower fees per session. The new 

format began to be offered after the first 129 participants had 

20 

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been assigned to 26-week groups. From 8/15/95 until the end of 

intake, defendants were offered a choice between 8-week and 26-week 

formats. In practice, no one chose the 26-week option once the 8- 

week groups became available. Thus, the final 61 ATV participants 

were assigned to the 8-week groups. 

0 

Community service Defendants rejected by lottery from 

batterer treatment were mandated by judges to participate in 70 

hours of cornunity service. Typically, the service was performed 

over a two-week period. I 

hours were arranged over 

could continue their jobs 

3r offenders who were employed, flexible 

a two-month period in order that they 

3 

Participants were assigned to work on 

renovating housing units, clearing vacant lots to make way for 

community gardens, painting senior citizen centers, and cleaning up 

playgrounds -- all activities which would not be expected to impact 

on abusive behavior. In the course of their service, participants 

0 were given education about drugs and HIV. Interested individuals 

were also referred to drug, HIV, or employment counseling programs. 

21 

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Participants in both batterer treatment and community service 

programs were expelled from the programs if a pattern of nonattendance developed (for ATV, three misses constituted grounds for 

dismissal from the program). For the men assigned to batterer 

treatment, such bases were referred to the prosecutor's office for 

0 

action. At the discretion of the district attorney's office, 

delinquent cases were returned to the court calendar and -new 

sentences could be imposed. In practice, few cases were actually 

restored to the calendar because the period of court supervision 

s 

typically was drawing to a close by the time a clear pattern of 

non-compliance was established and a restoral request was 

completed. 

Follow-up on delinquents was more reliable for the community 

service group. The organization running that program had the 

ability to place cases of delinquents on the court calendar 

themselves, rather than reco-mending to the prosecutor that cases 

0 

be restored. If the court issued an arrest warrant for noncompliance, the community service program had enforcement staff who 

executed the warrants. 

Assianment Process and Case Intake 

Cases were drawn from three of eight post-arraignment parts in 

Kings County Criminal Court. Two of the parts were specialized 

domestic violence parts. The third was the jury trial part where 

domestic violence and other cases were transferred if a negotiated 

disposition could not be reached. At the point at which judge, 

22 

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prosecutor, and defense had reached agreement on batterer treatment 

as an appropriate disposition, defendants were screened by Atv for 

eligibility and then randomly assigned to batterer treatment or 

community service. Defendants assigned to batterer treatment were 

given a start date (usually within a week of intake) and directions 

to the class. 

After assignment to treatment, the defendant was accompanied 

back to the courtroom and the prosecutor informed of the lottery 

assignment. The prosecutor informed the judge who then accepted a 

s 

disposition consistent with the assignment. In 28% of control 

cases judges overrode the lottery decision to deny batterer 

treatment and mandated the ATV program for defendants who had been 

assigned to community service. There were no judicial overrides of 

cases randomly assigned to the ATV program. 

a 

Follow-Up Measures 

Because the most important outcome of treatment is reduction 

of violence, we included several measures of new violence in 

victim-batterer relationships. The violence measures were: new 

incidents involving the same victim which were reported to criminal 

justice authorities and reports by victims of new incidents to 

research interviewers. These indicators have become commonly-used 

in studies which track households where domestic violence occurs, 

for example, in NIJ's SARP research (see, for example, Fagan, 

Garner, and Maxwell, 1995). Violence indicators do not always 

behave in similar ways (see, for example, Davis and Taylor, 1997), 

23 

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so it is important to capture more than one. Both measures were 

captured at 6 and 12 months after the time that batterers were 

sentenced. Victim self-reports were obtained through (primarily) 

telephone interviews. Crime report and arrest data were obtained 

from official records. 

In addition to capturing information on new violent acts, the 

interviews also assessed attitudinal and cognitive behaviors among 

batterers and victims. For both groups we measured attitudes 

toward violence in the family and conflict resolution skills. We 

also measured for both batterers and victims whether their 

cognitive styles tended toward internal or external locus of 

control.1 That is, did they believe that they could influence 

events or did they believe that things happened to them? It seemed 

plausible that, if batterer treatment succeeded in engendering in 

batterers a greater sense of responsibility for their actions, they 

would become more internal on locus of control. Finally, the 

interview schedules included for victims only measures of 

psychological adjustment. If treatment of the batterer led to 

changes in the way that they acted toward their partners then, we 

believed, that women's self-esteem and sense of well-being might 

improve. 

-. 

1 Cognitive measures included the Inventory of Beliefs about Wife 

Beating Scale" (Saunders, Lynch, Grayson and Linz, 1987); 

Harrell's (1991) measure of Conflict Resolution Skills; and a. 

shortened (12-item) version of the Nowicki-Strickland InternalExternal Control Scale (Nowicki and Duke, 1974). 

24 

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Interview Methodoloav 

We attempted interviews with defendants and victims on three 

occasions: (a) at case intake (date of court disposition), (b) six 

months after intake, and (c) twelve months after intake. 

Interviews with batterers were conducted in person in the court 

building just prior to assigning them to either batterer treatment 

or community service. In subsequent interviews with batterers and 

all interviews with victims, telephone was the modality of choice. 

Because we considered the victim interviews more accurate than 

batterer interviews for assessing new violence, we put special 

efforts into interviewing victims. When telephone attempts failed, 

we sent teams of interviewers to victims' homes. If the home 

interview attempts also failed, we mailed letters offering first 

$25 and then $50 for completion of an interview. In the third 

interview wave for victims we turned over 70 difficult cases to a 

licensed private investigator as a last resort. The private 

investigator used available computer databases to track victims who 

had moved and provide us with current addresses. He did not 

confront victims or their acquaintances, and interviews for women 

he located were conducted by our staff over the phone. Ultimately, 

this additional tracking methodology added virtually nothing to the 

interview success rate. 

3 

0 

Completion rates Our completion rate with victims 

was 50% for the first interview, 46% for the second interview, 

and 50% for the third interview. First interviews with batterers 

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were obtained with 95% of the sample because interviews were 

obtained when defendants were present at intake in court for the 

treatment program. Subsequent completion rates were 40% for the 

second interview and 24% for the third interview. The fact that 

attrition among victim interviews was substantially lower than 

among batterers results from the extra lengths (incentives, inperson visits) to which we went in order to obtain the victim 

interviews. 

3 

26 

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FINDINGS AND CONCLUSIONS 

Our initial analyses showed that men assigned to a group 

treatment program for batterers were less likely to be the subject 

of future crime complaints involving the same parties than men . 

assigned to an irrelevant treatment (community service). This 

difference was most pronounced at six months after group 

assignment, but held up over a full year (see Table 5). 

J 

Subsequent analyses revealed interesting findings about length 

of treatment. Due to fortuitous circumstances, we wound up 

splitting our treatment sample into two subsamples distinguished by 

density of treatment sessions. All batterers randomly assigned to 

treatment were mandated to attend 39 hours of psycho educational 

group treatment based upon the Duluth model. However, some 

batterers received the 39 hours in 26 weekly sessions while others 

received it in longer biweekly sessions for 8 weeks. The former 

treatment model maximized time that batterers remained in treatment 

while the latter reduced the chances that batterers' initial 

motivation would flag over time. 

0 

Our results showed that far more men successfully completed 

the 8-week group than the 26-week group (see Table 6). Roughly 

similar proportions of batterers began treatment in the 8-week and 

26-week groups. Seventy-seven percent of those assigned to the 8- 

week groups attended at least one class compared to 71% of those 

27 

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Table 5: Prevalence of criminal justice incidents involving same victim and perpetrator. 

* Chi-square (1)=10.43, p.=.OOl 

**. Chi-square (1)=7.78, p.=.005 

Table 9: Prevalence of incidents reported by victims to research interviewers. 

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I 

26-week format 

(n=129) 

8-week format 

(n=61) 

I Table 6: Attendance in 8 vs 26 week batterers’ group 

29% 44% 21 % 

23 % 10% 67 % 

I No attendance ~ ~~ rime attendance I Graduated 

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assigned to the 26-week groups. But graduation rates were 

dramatically different. Sixty-seven percent of the men assigned to 

the 8-week groups graduated compared to just 27% of those assigned 

to the 26-week groups.2 guessed We conclude that a much larger 

proportion of those assigned to treatment were exposed to the full 

treatment in the 8-week groups than in the 26-week groups. 

We expected, therefore, that men assigned to the 8-week 

group would have a lower rate of recidivism than men assigned to 

the 26-week group. However, only the 26-week group was 

statistically different from the control group on future crime 

complaints at both 6 and 12 months post-sentence: The 8-week group 

and the control group were indistinguishable (see Table 7). 

Victim reports of violence to research interviewers showed a 

similar pattern, but differences between treatment conditions did 

not approach statistical significance (see Table 8). 

3 

,The three-group comparisons also were run using multivariate 

models, and the results are presented in Appendix A. In the 

multivariate models, treatment effects were assessed after 

controlling for the effects of defendant age, ethnicity, marital 

status, employment status, and arrest history. A1 though 

introducing control variables is not, strictly speaking, necessary 

in analyzing data from experiments, doing so increases the 

precision of statistical tests (Patel, 1996; Armitrage, 1996). The 

results of two multivariate models using the number of new 

’ Chi-square (1)= 27.72, p < .001. 

28 

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Table 7. Prevalence of criminal justice incidents involving same victim and perpetrator. 

6 months after assignment* 

26-week batterer treatment 7% 

(n= 129) 

8-week batterer treatment 15% 

(n=61) 

12 months after assignment** 

10% 

25 % 

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a 6 months after assignment* 12 months after 

assignment** 

26-week batterer treatment 23% 14% 

(n=52) (n=66) 

8-week batterer treatment 19% 18% 

(n=26) (n=33) 

Control (community 21% 22% 

service) (n=93) (n=90) 

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incidents reported to criminal justice authorities and the number 

of new incidents reported by victims to research interviewers 

support the conclusions in the paragraph above. In addition, an 

0 

analysis of time to failure using criminal justice data also shows 

a significant effect of the 26-week treatment. 

Finally, we examined measures of the cognitive change in 

batterers, including conflict resolution skills, beliefs about 

domestic violence, and locus of control Means and standard 

deviations for each of the three tests at each of the two time 

3 

points are presented in Table 9. For each scale, means across the 

three treatment groups are remarkably similar, and none of the 

tests shown in Table 9 come close to statistical significance. We 

have, therefore, no basis for claiming that treatment changed 

batterers' attitudes or ways of dealing with conflict. But we note 

that serious limitations in the scales and in our data do not 

permit an adequate test of this hypothesis. (For a discussion of 

limitations, the reader is referred to the full report.) 

***** 

Batterer intervention can be looked upon in one of two ways. 

It may be a learning process in which attitudes and behavior are 

modified in a relatively permanent way, Or it may be that batterer 

intervention simply suppresses violent behavior for the duration of 

treatment, but no permanent changes are effected. Our results do 

not support the model of treatment as a change process: If that 

were true, then the men in the 8-week group (who were finished with 

29 

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*Numbers on parentheses are standard deviations. 

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treatment long before the follow-up period was up) ought to have 

been as non-violent as their 26-week counterparts (who were in 

treatment for most of the follow-up period). Yet that is not what 

our results showed. Also, we did not find evidence that treatment 

altered attitudes toward spouse abuse, further suggesting that 

there was no basis for permanent changes. (However, the reader is 

again advised of serious limitations in the cognitive change scales 

and data.) 

Our results, then support the suppression model of bataterer 

intervention. But they are only suggestive since the study was not 

designed to test the validity of various models of the treatment 

process. Moreover, they are at odds with other studies which have 

not tended to find a difference in recidivism according to length 

of treatment (Edelson and Syers, 1990; Gondolf, 1997a). Many 

current batterer programs are going to longer treatment models, but 

there is also substantial pressure from the defense bar and 

economics to keep time in treatment to a minimum. Thus, the 

question of whether treatment works only as long as men attend 

groups is key to intelligent policy formulation. 

0 

How do our results fit into the literature on batterer 

treatment? If we concentrate only on the four quasi- and two true 

experiments (including ours), then we note that five of the six 

(Harrell, et. al. is the lone exception) reported results in the 

expected direction and all reported statistical significance on at 

least one outcome measure. 

Taken together, these studies provide a case for rejecting the 

30 

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nu a 

Taken together, these studies provide a case for rejecting the 

1 hypot iesis that treatment has no effect on violent behavior 

toward spouses. However, the number of useful studies is small and 

more well-designed studies are warranted before coming to firm 

conclusions. 

Our study provides a good illustration of the difficulties 

that can be encountered implementing a true experimental design. We 

had to make substantial concessions to court officials in order to 

gain their cooperation. Judges were allowed to override assigsments 

to the control group in exceptional cases. This produced a high 

rate of judicial overrides of cases assigned to the control group. 

As we showed in the last chapter, the effect of including the 

override cases in the control group was to make the tests of 

treatment effects more conservative. (Yet, we still found large 

treatment effects. ) Also, we had to offer a treatment alternative 

that was more palatable to the defense than the lengthy and costly 

version that we started with. This proved to be a fortuitous 

change, however, since we found substantial differences in outcomes 

between men assigned to the 8-week and 26-week groups. We agree 

with the opinion of Fagan (1996) and most serious researchers, 

however, that the benefits of random assignment outweigh the 

potential difficulties. 

0 

31 

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APPENDIX A 

RESULTS OF MULTIVARIATE ANALYSES 

1 

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TABLE A-1 

Poisson Regression of Annual Rate of Any Officially Recorded Offense 

Model 1 Model 2 Model 3 Model 3 

Model Parameters b s.e. Exp(B) b s.e. Exp(8) b s.e. Exp(8) b s.e. Exp(B) 

AN 

Short -0.24'0.30 0.8 -0.24 0.29 0.8 -0.28 0.46 0.8 0.02 0.35 1.0 

Long -0.58 0.24 0.6 -0.57 0.24 0.6 -0.30 0.34 0.7 -0.90 0.36 0.4 ' 

Age 

Ethnicity(African-American) 

West IndianlCari bbean 

Other Race 

I Hispanic 

Married 

Employed 

Prior Arrest 

ATV Employment 

Short Employment 

Long Employment 

0.00 0.01 1.0 0.00 0.01 1.0 0.00 0.01 1.0 

-0.29 0.25 0.7 -0.28 0.25 0.8 -0.28 0.25 0.8 

-0.47 0.30 0.6 -0.47 0.30 0.6 -0.45 0.30 0.6 

-0.33 0.32 0.7 -0.32 0.32 0.7 -0.31 .0.32 0.7 

0.19 0.20 1.2 0.22 0.20 1.2 0.14 0.26 1.1 

0.35 0.20 1.4 0.36 0.20 1.4 0.38 0.20 1.5 

-0.24 0.21 0.8 -0.12 0.26 0.9 -0.28 0.21 0.8 

0.07 0.58 1.1 

-0.52 0.49 0.6 

AN Married 

Short ' Married -0.65 0.60 0.5 

Long ' Married 0.66 0.49 1.9 

c " -1.03 0.43 Intercept -1.10 0.13 -1.08 0.43 -1.17 0.44 t 

Model Fit 

Log likelihood -241.71 -236.52 -235.88 -234.52 . Restricted Log likelihood -244.89 -244.89 -244.89 -244.89 

Chi-square 6.36 16.74 18.02 20.75 

P-value 0.04 0.05 0.08 0.04 

I 

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TABLE A-2 

Negative Binomial Regression of the Past - Two .. Month --- Frequericy -. of Victimization @ Six Month Survey 

Model I Model 2 Model 3 Model 3 

Model Parameters b s.e. Exp(f3) b. s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(6) 

ATV 

Short 

Long 

-1q.53 1.34 0.2 

-0.88 0.90 0.4 

Age 

Et hnici ty (African-American) 

Hispanic 

West IndianlCaribbean 

Other Race 

Married 

Employed 

Prior Arrest 

An/ Employment 

Short Employment 

Long ' Employment # 

- AN Married 

Short Married 

Long ' Married 

-1.12 1.43 .0.3 

-1.02 0.91 0.4 

0.04 0.08 1.0 

-1.39 

-0.44 

1.11 

1.38 1.11 4.0 

0.32 1.25 1.4 

0.96 1.84 2.6 

.24 0.2 

.02 0.6 

.I4 3.0 

0.49 2.72 1.6 

-0.74 1.12 0.5 

0.06 0.08 1.1 

1.68 1.25 5.4 

0.11 1.29 1.1 

1.04 1.96 2.8 

-1.52 1.27 0.2 

0.23 1.312 1.3 

0.82 1.14 2.3 

-2.93 2.16 0.1 

-1.05 1.28 0.3 

0.05 0.08 1.0 

1.36 1.09 3.9 

0.13 1.45 1'.1 

0.66 1.96 1.9 

-1.74 1.45 0.2 

-0.36 1.04 0.7 

1.24 1.12 3.5 

-2.63 3.39 0.1 

-0.68 1.73 0.5 

2.58 2.96 13.1 

-0.02 1.92 1.0 

Intercept -4.79 7.63 -7.95 6.94 -10.75 8.94' 

Selection Bias ratio 6.45 9.07 8.15 8.38 10.34 10.31 

Scalar 11.04 3.30 8.81 2.47 ttt *.C 9.0 2.46 **b 

-7.57 6.81 

7.48 8-18 t*. 8.72 2.40 , 

. Model Fit 

Lon likelihood -1 99.21 77 -1 93.87 -I 92.77 -1 92.77 

-474.46 -473.1 3 -468.86 

Chi-square 694 561 .I 8 560.41 552.1 8 

Restricted Log likelihood -545.7404 

P-value * 0.00 0.00 0.00 0.00 I 

a 

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TABLE A-3 

- Model 1 Model 2 Model 3 Model 3 

Model Parameters b s.e. Exp(8) b s.e. Exp(B) b s.e. Exp(B) b s.e. - Exp(8) I 

AN 

Short 

Long 

Age 

Et hniaty(African-American) 

Hispanic 

West IndianlCaribbean 

Other Race 

Married 

Employed 

Prior Arrest 

-0.94’ 1.01 0.4 

-1.29 0.81 0.3 . 

-2.10 1.66 0.1 I 

-0.79 1.18 0.5 -2.16 2.29 0.1 

-1.57 1.07 0.2 -1.70 1.47 0.2 -0.95 1.12 0.4 

AN ’ Employment 

Short ’ Employment 

Long Employment 

AWL Married 

Short Married 

Long Married 

01.02 0.05 1.0 0.01 0.05 1.0 0.01 0.05 1.0 

1 .o 

-0.85 1.06 0.4 -0.57 1.29 0.6 -0.51 1.21 0.6 

0.34 1.18 1.4 0.43 1.44 1.5 0.51 1.36 1.7 

0.10 1.69 1.1 0.00 1.85 1.0 -0.02 1.61 1.0 

-0.86 1.30 0.4 -0.98 1.28 0.4 -0.51 1.17 0.6 

-0.80 1.18 0.4 -1.18 1.41 0.3 -1.00 1.12 0.4 

-1.03 0.92 0.4 -0.83 0.96 0.4 -0.90 0.93 0.4 

2.06 2.90 7.8 

0.20 2.11 1.2 

1 .o 

1 .o 

1 .o 

1 .o 

1.90 2.47 6.7 

-3.52 2.82 0.0 

Intercept 1.62 7.93 4.41 9.14 ‘ 3.56 9.60 * 5.49 9.21 

Scalar 13.92 3.36 44t 11.97 3.34 444 11.65 3.36 10.35 2.98 

Selection Bias ratio -1.02 10.12 -3.98 11.51 -2.27 12.12 -5.14 11.49 a44 444 

Model Fit 

Log likelihood -1 91.03 -1 87.30 -1 86.44 -1 82.28 

Restricted Log likelihood -61 7.99 -551.84 -546.37 -529.49 

Chi-square . 853.92 729.09 71 9.85 694.43 

P-value 0.00 0.00 0.00 0.00 

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TABLE A-4 

Cox Regression Model of Time-to-first New Officialiy -- Recorded Offenses Against Same Victim 

Model 1 Model 2 Model 3 Model 4 Model 5 

Model Parameters b s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(B) b s.e. Exp(6) b s.e. Exp(B1 

ATV 

Short -0.21 0.291 0.8 -0.52 0.64 0.G -0.15 0.30 0.9 -0.16 0.47 0.9 0.108 0.36 1.1 

Long -0.72 0.26 0.5 " -1.36 0.63 0.3 -0.74 0.26 0.5 " -0.75 0.39 0.5 ' -0.96 0.36 0.4 '* 

An/ 

Short Time 

Long Time 

Age 

Ethnicity(African-American) 

Hispanic 

West IndianKaribbean 

Other Race 

Married 

Employed 

Prior Arrest 

ATV Employment 

Short Employment 

Long Employment 

An/ Married 

Short * Married 

Long Married 

0.00 0.00 1.0 

0.00 0.00 1.0 

0.01 0.01 1.0 0.01 0.01 1.0 0.01 0.01 1.0 

-0.26 0.26 0.8 -0.26 0.26 0.8 -0.27 0.26 0.8 

-0.50 0.31 0.6 -0.50 0.31 0.6 -0.50 0.31 0.6 

-0.76 0.39 0.5 '+ -0.76 0.39 0.5 ' -0.74 0.39 0.5 ' 

0.09 0.22 1.1 0.09 0.22 1.1 0.05 0.26 1.0 

-0.28 0.22 0.8 -0.27 0.26 0.8 -0.32 0.22 0.7 

0.53 0.22 1.7 *+ 0.53 0.22 1.7 * 055 0.22 1.7 

0.01 0.60 1.0 

0.03 0.53 1.0 

/ 

-0.65 0.62 0.5 

0.50 0.53 1.6 

Model Fit 8 

Log likelihood 1035.47 1035.47 1035.47 1035.47 1035.47 

Restricted Log likelihood 1027.1 'I 1025.58 101 0.80 101 0.79 1008.15 . 

Chi-square 7.90 9.1 5 24.40 24.80 7.903 

P-value 0.02 0.05 0.00 0.01 0.02 

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