National Institute on Drug Abuse

RESEARCH

MONOGRAPH SERIES

Statistical Issues

in Clinical Trials

for Treatment of

Opiate

Dependance

U.S. Department of Health and Human Services • Public Health Service • National Institutes of Health

128
Statistical Issues in Clinical

Trials for Treatment of Opiate

Dependence

Editor:

Ram B. Jain, Ph.D.

NIDA Research Monograph 128

1992

U.S. DEPARTMENT OF HEALTH AND HUMAN SERVICES

Public Health Service

Alcohol, Drug Abuse, and Mental Health Administration

National Institute on Drug Abuse

5600 Fishers Lane

Rockville, MD 20857
ACKNOWLEDGMENT

This monograph is based on the papers and discussions from a technical

review on “Statistical Issues in Clinical Trials for Treatment of Opiate

Dependence” held on December 2-3, 1991, in Bethesda, MD. The technical

review was sponsored by the National Institute on Drug Abuse (NIDA).

COPYRIGHT STATUS

NIDA has obtained permission from the copyright holders to reproduce certain

previously published material as noted in the text. Further reproduction of this

copyrighted material is permitted only as part of a reprinting of the entire

publication or chapter. For any other use, the copyright holder’s permission

is required. All other material in this volume except quoted passages from

copyrighted sources is in the public domain and may be used or reproduced

without permission from the Institute or the authors. Citation of the source is

appreciated.

Opinions expressed in this volume are those of the authors and do not

necessarily reflect the opinions or official policy of the National Institute on Drug

Abuse or any other part of the US. Department of Health and Human Services.

The U.S. Government does not endorse or favor any specific commercial

product or company. Trade, proprietary, or company names appearing in this

publication are used only because they are considered essential in the context

of the studies reported herein.

NIDA Research Monographs are indexed in the “Index Medicus.” They are

selectively included in the coverage of “American Statistics Index,” “BioSciences

Information Service,” “Chemical Abstracts,” “Current Contents,” “Psychological

Abstracts,” and “Psychopharmacology Abstracts.”

DHHS publication number (ADM)92-1947

Printed 1992

ii
Contents

Introduction

Ram B. Jain

Drug Dependence (Addiction) and Its Treatment

Frank J. Vocci, Jerome H. Jaffe, and Ram B. Jain

Background and Design of a Controlled Clinical Trial

(ARC 090) for the Treatment of Opioid Dependence

Rolley E. Johnson and Paul J. Fudala

Page

1

6

14

Clinical Endpoints: Discussion Session 25

Ram B. Jain

Design of Clinical Trials for Treatment of Opiate Dependence:

What Is Missing? 29

Ram B. Jain

Comments 37

Sudhir C. Gupta

Rejoinder 42

Ram B. Jain

Summary of Discussion 44

Ram B. Jain

iii
Efficacy of Urinalysis in Monitoring Heroin and Cocaine

Abuse Patterns: Implications in Clinical Trials for

Treatment of Drug Dependence 46

Edward J. Cone and Sandra L. Dickerson

Comments 59

Nancy L. Geller

Summary of Discussion 62

Ram B. Jain

Open/Panel Discussion: Design Issues 64

Ram B. Jain

A Bayesian Nonparametric Approach to Analysis of Treatment for

Drug Dependence Data 7 0

Ram C. Tiwari

Three Estimators of the Probability of Opiate Use From

Incomplete Data 82

Alan J. Gross

Summary of Discussion 95

Ram B. Jain

Issues in the Analysis of Clinical Trials for Opiate Dependence 97

Dean Follmann, Margaret Wu, and Nancy Geller

Summary of Discussion 114

Ram B. Jain

Analysis of Clinical Trials for Treatment of Opiate Dependence: What

Are the Possibilities? 116

Ram B. Jain

Summary of Discussion 135

Ram B. Jain

Toward a Dynamic Analysis of Disease-State Transition Monitored by

Serial Clinical Laboratory Tests 137

T.S. Weng

iv
Summary of Discussion 158

Alan J. Gross

A Markov Model for NIDA Data on Treatment of Opiate Dependence 160

Mei-Ling Ting Lee

Summary of Discussion 168

Alan J. Gross

Open/Panel Discussion: Analysis Issues 170

Ram B. Jain

Open/Panel Discussion: General Issues 176

Ram B. Jain

List of Participants 182

List of NIDA Research Monographs 186

v

Introduction

Ram B. Jain

The Medications Development Division (MDD) of the National Institute on

Drug Abuse (NIDA) came into existence in August 1990. Its mandate from

the U.S. Congress is to develop medications for the treatment of drug

dependence, primarily heroin and cocaine dependence. The organizational

structure of MDD allows for five branches, one of which is the Biometrics

Branch. I happened to be the first one to join the Biometrics Branch, and

it was and still is a great learning opportunity for me. I found: Drug

dependence is not a disease in the traditional sense that cancer or heart

disease is; its treatment is not a treatment in the traditional sense-drug

dependence is not treated the way a cancer or an infection is treated; and

the characteristics of the data generated by clinical studies in drug abuse

area are unique, not seen in other branches of medicine-a more than 50-

percent dropout rate! The data generated by these studies are the product

of a continuous dynamic interaction between the pharmacological effect of the

therapeutic agent, the effect of nonpharmacological services provided as part

of the total treatment, and most importantly, the drug-seeking behavior of the

addict, which is shaped and influenced by the environmental stimuli around

him or her. How does one statistically adjust for this multidimensional “noise”?

What is being treated here is not quite obvious-Is it a medical condition, a

mental disorder, a behavioral abnormality, or all of them at the same time?

Between September 1988 and May 1990, Drs. Rolley E. Johnson and Paul J.

Fudala conducted a randomized double blind, “double dummy” clinical trial

(ARC 090) to evaluate the efficacy of 8 mg sublingual doses of buprenorphine

compared with 20 mg and 60 mg oral doses of methadone in 162 patients.

This study was conducted at NIDA’s Addiction Research Center (ARC).

These data were provided to me for analysis. The primary data consisted

of binary (positive vs. negative) data points obtained by assaying the urine

samples for the presence of opiates. Since the urine samples were obtained

three times a week from each patient in this 25-week study, each patient could

provide up to 75 data points. Many endpoints could be defined and clinically

defended using these data (e.g., percent-positive samples; a drug-free period

of, say, 28 days or more), and several different statistical methods could be

used to analyze them. After spending several months with these data, finding

1
myself more informed every day than the day before, I determined that more

could be learned—I could use expert opinion from outside.

During the summer of 1991, I began planning for a workshop (a NIDA

technical review) in design and analysis of clinical trials in the treatment of

opiate dependence. Many well-known statisticians, including those who had

many years of experience in managing and analyzing clinical trials, were

contacted and asked if they would like to write and present research papers on

the design and analysis of clinical trials in the treatment of opiate dependence

and/or participate in this workshop. Commitments were obtained for five

research papers. Each paper was to present the results of analyzing a part

of the ARC 090 data. I also decided to present two papers-one on design,

one on analysis. The statisticians who agreed to write research papers and/or

participate (and finally came to the workshop) included Drs. Joseph Collins

(Veterans’ Administration Medical Center), Lloyd D. Fisher (University of

Washington), Dean Follmann (National Heart, Lung, and Blood Institute

[NHLBI]), Nancy L. Geller (NHLBI), Albert J. Getson (Merck Sharp & Dohme),

Joel B. Greenhouse (Carnegie-Mellon University), Alan J. Gross (Medical

University of South Carolina), Sudhir C. Gupta (Northern Illinois University),

A.S. Hedayat (University of Illinois), Nicholas P. Jewell (University of California

at Berkeley), Peter A. Lachenbruch (University of California, Los Angeles),

Jack C. Lee (National Institute of Child Health and Human Development

[NICHD]), Mei-Ling Ting Lee (Boston University), Shou-Hua Li (National

Institute of Dental Research), Taesung Park (NICHD), Carol K. Redmond

(University of Pittsburgh), Saul Rosenberg (NIDA), Vincent Shu (Abbott

Laboratories), Richard Stein (Food and Drug Administration [FDA]),

Ram C. Tiwari (University of North Carolina), L.J. Wei (Harvard School

of Public Health), T.S. Weng (FDA), and Margaret Wu (NHLBI).

Without the presence, interaction, guidance, and advice of clinicians working

in the drug abuse area, talking about designing and analyzing clinical trials

for treatment of drug dependence would have been an exercise in futility,

and therefore we requested participation from well-known clinicians in

government, industry, and academia. Those who agreed to participate (and

came to the workshop) included Jack D. Blaine (NIDA), Robert J. Chiarello

(NIDA), Edward J. Cone (ARC), Paul J. Fudala (University of Pennsylvania),

Harold Gordon (NIDA), David A. Gorelick (ARC), Charles W. Gorodetzky

(CIBA-Geigy Corporation), Charles V. Grudzinskas (NIDA), John Hyde (FDA),

Donald R. Jasinski (Johns Hopkins University), Rolley E. Johnson (Johns

Hopkins University), Michael Murphy (Hoechst Roussel Pharmaceutical,

Inc.), Frank J. Vocci (NIDA), and Curtis Wright (FDA).

2
The NIDA technical review on “Statistical Issues in Clinical Trials for Treatment

of Opiate Dependence” took place on December 2-3, 1991, at the Bethesda

Marriott, Bethesda, MD. It consisted of four sessions: a Clinical Session, a

Design Session chaired by Dr. Gross, a two-part Analysis Session chaired

by Drs. Wei and Fisher, respectively, and a General Issues Session cochaired

by Drs. Lachenbruch and Jack C. Lee. Drs. Vocci and Johnson presented

papers during the Clinical Session; Dr. Cone (with Sandra L. Dickerson) and

I presented papers during the Design Session; and Drs. Follmann (with Drs.

Geller and Wu), Gross, Gupta, Mei-Ling Ting Lee, Weng, and I presented

papers during the Analysis Session. All papers presented during the Design

and Analysis Sessions were available for precirculation and were peer reviewed

prior to the meeting. Authors were also invited to write rejoinders to referees’

comments. Drs. Geller, Greenhouse, Gross, Gupta, Jewell, Jack C. Lee,

Redmond, and Tiwari were the reviewers. After the authors had presented

their papers, reviewers also presented their comments at the workshop.

Following the reviewers’ comments and rejoinders, if any, there

was an open brief discussion of each paper that was presented.

Individual papers during the Clinical Session were followed by a Discussion

Session. The aim of this discussion session was to have the opinion of FDA

about what kind of endpoints would be adequate and/or appropriate in clinical

trials for treatment of drug dependence, what statistical methods should be

used to analyze the data generated from these trials, and in general, what

should be the strategy used to design these trials? The discussants for this

session were Drs. Hyde, Gorodetzky, Stein, and Wright.

All three Statistical Sessions concluded with a combined open/panel discussion.

At each of these discussion sessions, a series of questions were presented

(by NIDA) to the panels for discussion. Additional questions as appropriate

were allowed to be presented by any of the participants at the workshop. The

members of the Design Panel were Drs. Hedayat (chair), Getson, Gross, Gupta,

Jasinski, Mei-Ling Ting Lee, Redmond, and Wu. The members of the Analysis

Panel were Drs. Redmond (chair), Fisher, Follmann, Greenhouse, Gross, and

Hedayat. The members of the General Issues Panel were Drs. Lachenbruch

(cochair), Jack C. Lee (cochair), Collins, Fisher, Gupta, Jewell, Murphy, Shu,

and Tiwari.

I was honored to organize and be a participant in this NIDA technical review.

The workshop was a tremendous success. There was a free exchange of

opinion and information between the statisticians and clinicians. There were

more agreements than disagreements. There was a unanimous agreement:

These trials need a lot more work in both the design and analysis areas.

However, in the unbiased opinion of a very prominent statistician, not

3
connected with NIDA in any way to the best of my knowledge, one of the

papers presented at this workshop was what might be called a breakthrough.

This monograph presents the revised manuscripts as provided by the authors.

Some of the revisions in these manuscripts may be a direct result of referees’

comments and authors’ rejoinders. Consequently, except for two papers,

referees’ comments and/or authors’ rejoinders are not being reproduced, but

all the referees have been given credit for their comments. Dr. Tiwari, who

reviewed Dr. Gupta’s paper, showed interest (after the workshop) in writing

a paper. His paper is also included in this monograph. However, Dr. Gupta

could not submit an acceptable revised manuscript in time for publication

of this monograph. Consequently, his manuscript could not be included in

the monograph.

Summaries of discussions on individual papers presented in the statistical

sessions are also presented. Dr. Gross prepared the summary of discussions

that followed the papers by Drs. Mei-Ling Ting Lee and Weng. I prepared all

other summaries. I also prepared the summaries for the discussion session

that took place during the Clinical Session and for the open/panel discussions

during the Statistical Sessions. I have tried to give credit to individual speakers/

participants to the best of my ability. I have tried to reproduce opinions as close

to the those of individual speakers as possible. I have tried not to inject my own

biases to the degree I could. However, I take responsibility for all errors and

omissions and tender my apologies to those whom I may have misrepresented

and/or offended.

This is just a beginning. NIDA’s MDD is busy planning the development of

or is in the process of developing a variety of medications for the treatment of

cocaine, heroin, and other substances that have the potential for abuse. In

addition to buprenorphine (to treat heroin abuse), for which a multicentered

pivotal trial is ongoing, a trial for I-alpha-acetylmethadol (LAAM) (to treat heroin

abuse) will soon be initiated. This LAAM trial should lead to approval for its

marketing by FDA sometime in late 1992 or early 1993. A pivotal trial for a

sustained release formulation of naltrexone should be under way sometime in

1993. There are definite plans for developing a combination formulation of

buprenorphine and naltrexone. New compounds are being acquisitioned from

industry and elsewhere and are being tested for their potential for treatment of

drug abuse.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

4
Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

5
Drug Dependence (Addiction) and Its

Treatment

Frank J. Vocci, Jerome H. Jaffe, and Ram B. Jain

INTRODUCTION AND SOME DEFINITIONS

What is drug dependence or drug addiction? How does one become an

addict or dependent on a drug? There is no simple or single answer to these

questions. Dependence and addiction are the terms often used synonymously

(as they are in this chapter). Unfortunately, these terms are often used in

different ways in different contexts. Furthermore, according to Jaffe (1992):

. . . science has been given no exclusive right to the use

of [these] terms . . . . Among the many behaviors that have

been labeled “addictions” in the mass media are: eating salt;

buying lottery tickets; using gasoline, computers, or foreign

capital; taking educational courses; watching television;

running; and engaging in sex. Some of the uses of the term

are deliberately metaphorical.

This chapter, however, attempts to summarize how dependence or addiction

is currently viewed by most psychiatrists, physicians, and many behavioral

psychologists.

Although the concept of dependence has historically been divided into

psychological dependence and physical (physiological) dependence, the

current approach recognizes that such terms tend to contribute to an

unscientific dualism. Today, most researchers believe that the mind does

not exist independently of the brain. Drug dependence involves body, brain,

and behavior as influenced by the environment. Abuse of drugs does not

necessarily constitute drug dependence. One may keep abusing a drug but

may never be dependent on it and may never need to take it to feel normal.

For someone to change from being a drug abuser who is nondependent to

someone who is drug dependent, the sense of control must change so that the

individual begins to feel a need to take the drug to feel normal, and therefore

the flexibility to use or not to use the drug is diminished. During this transition

6
from nondependeny to dependency, the pattern of drug abuse does not have

to change, although quite often there is an escalation in terms of the number

of times the drug is used or the amount that is used.

“Drug tolerance is a state of decreased responsiveness to the pharmacological

effect of a drug resulting from a prior exposure to that drug or a related drug.

When exposure to drug A produces tolerance to it and also to drug B, the

organism is said to be cross-tolerant to drug B” (Goldstein et al. 1974). Drug

tolerance can occur because of alterations in the central nervous system or

because of more rapid metabolism (usually by hepatic induction). Although still

used, “physical dependence” is another term that conveys a sense of sharp

distinction between the brain and the “mind.” Physical dependence is used

to mean that the use of a given drug has produced an altered body physiology

so that, when the drug is stopped, there are physiological abnormalities (which

eventually pass) that can be prevented by continued use of the drug. Physical

dependence can be revealed by stopping the drug or by giving an antagonist

that displaces the drug from its site of action in the body. Physical dependence

can result from the therapeutic uses of a drug, for example, by using opioids

to relieve pain in cancer therapy or benzodiazepines to treat anxiety. The

discontinuation of a drug that one is physically dependent on can result in

various pathophysiologic disturbances collectively known as a withdrawal or

abstinence syndrome. It is entirely possible that an individual could be

physically dependent on a drug but still not be “addicted” to a drug; that is,

the appearance of withdrawal symptoms does not necessarily cause the

individual to continue using the drug. Then, what is drug dependence?

According to Goldstein and colleagues (1974), drug dependence consists

of three distinct and independent components: tolerance, physical

dependence, and drug-seeking behavior resulting in compulsive abuse

(psychic craving). Of course, these features are noticed in different degrees

in drug dependence on different drugs. In the case of some drugs, only one

or two of these components are noticed. “An example of tolerance and

physical dependence without compulsive abuse is provided by the morphine

congener and antagonist nalorphine” (Goldstein et al. 1974).

According to earlier concepts formulated in the 1930s, 1940s, and 1950s,

a drug was not considered to be addictive unless it produced physical

dependence characterized by an easily observable withdrawal syndrome.

This view led to popular misconceptions about the dependence potential

of both nicotine and cocaine. However, addiction is still an evolving concept.

Currently, many researchers and clinicians believe that life-threatening intensity

or easy observability of a withdrawal syndrome is not a necessary element in

addiction. For example, nicotine is believed to be addicting even though its

withdrawal syndrome is not dramatic and no one has ever died from its

7
withdrawal. An increasing trend in the diagnosis of dependence is to

characterize the addictive disorders in terms of the pattern of use, loss of

control over amounts ingested, and continued use despite medical, legal,

occupational, or interpersonal problems.

There are now two widely recognized sets of standard criteria that are used

to determine whether a given individual should be considered to be dependent

on a drug: the DSM-III-R criteria developed by the American Psychiatric

Association (1987) and the ICD-10 criteria developed by the World Health

Organization (1990). The DSM-III-R criteria for drug dependence include

behaviors that allow an observer to infer that the individual has a decreased

freedom to choose whether or not to use the drug. To be diagnosed as drug

dependent, a person must meet three of the following criteria (American

Psychiatric Association 1987):

Ingestion of larger amounts (of drug) or over a longer

period of time than intended, signifying loss of control over

behavior

Desire to or unsuccessful attempt to cut down drug use,

once again representing loss of control over behavior

Great deal of time spent in procuring drug and recovering

from its effects

Frequent intoxication or withdrawal when expected to fulfill

major role obligations at work, school, or home; i.e.,

interference with obligations of life; e.g., reinforcing things

in life like watching TV, reading books, interactions with

people etc.

Other activities given up or reduced due to substance use

Continued use despite problems at work, in life (e.g.,

marital problems) or legal problems

Marked tolerance

Characteristic withdrawal symptoms

Substance use to relieve withdrawal

8
In addition, these symptoms or behaviors must persist for more than 1 month.

Furthermore, drug dependence can be graded as mild, moderate, or severe

depending on the number of criteria met. A full remission means no use or use

with no dependence in the past 6 months.

The criteria used in ICD-10 are somewhat different. According to ICD-10, for

someone to be diagnosed as (drug) dependent, at least three of the following

should have been experienced or exhibited at some time during the previous

year (World Health Organization 1990):

A strong desire or sense of compulsion to take the

substance

An impaired capacity to control substance taking behavior

in terms of onset, termination or levels of use

Substance use with intention of relieving withdrawal

symptoms and with awareness that this strategy is

effective

Physiological withdrawal state

Evidence of tolerance such that increased doses of the

substance are required in order to achieve effects

originally produced by lower doses

Narrowing of the personal repertoire of patterns of

substance use

Progressive neglect of alternative pleasures or interests in

favor of substance use

Persisting with substance use despite clear evidence of

overly harmful consequences

However, neither of these sets of criteria is used by the Federal Government

for admission to a methadone maintenance program. According to Federal

regulations, dependence criteria for admission to a methadone maintenance

program are at least 1 year of addiction history, physiological addiction for at

least 1 year, andcontinuous or episodic addiction for most of the preceding

year (Methadone maintenance criteria 1989). It would be inappropriate to view

this as a formal definition of addiction; rather, it should be seen as specifying a

degree of addiction or opioid dependence that justifies admission to a

9
specialized program. In one sense, however, one could say that there is no

standard definition of drug dependence or any standard diagnostic test that

can be administered to classify a drug-dependent individual in need of

treatment. However, in the case of opioid dependence, there is a naloxone

challenge test that, by displacing opioids from the receptors in the brain, will

produce signs of physical dependence, that is, withdrawal symptoms, in anyone

who has been using opioids for a few days or longer. This test can also be

given to an individual who might be taking opioids for therapeutic purposes

(and will produce the same withdrawal symptoms after even a few doses of

opioids). Hence, the presence of a withdrawal syndrome (even a severe

one) does not necessarily mean the individual is addicted. The presence

of a withdrawal syndrome is neither necessary nor a sufficient condition for

the diagnosis of drug dependence. However, as noted above, in an individual

with a history of abuse, the presence of a withdrawal syndrome should be

documented when that person is seeking admission to a methadone

maintenance program. Hence, for the purpose of a clinical trial, the definition

(DSM-III-R or ICD-10) of dependence with or without additional criteria (e.g.,

naloxone challenge scores) can be used. Using DSM-III-R criteria allows

entrance into clinical trials of patients who would not necessarily meet criteria

for admission to a methadone maintenance program.

TREATMENT OF OPIOID ADDICTION

There are more than 1 million opioid abusers in the United States who can

possibly benefit from a treatment program. Of these, about 110,000 are in

methadone maintenance programs, and about 3,000 are in naltrexone

treatment. Many others are treated in detoxification programs, therapeutic

communities, and 12-step, drug-free programs; it is likely that the overwhelming

majority of this population are not participating in any kind of treatment.

Although pharmacologically based treatments are only one approach to

treatment, this approach plays an important role in the American system.

There are primarily two pharmacological approaches to treatment of opioid

dependence: agonist therapy and antagonist therapy.

Agonist therapy for opioid dependence constitutes replacing the abused

opioid with another, most likely a synthetic, opioid (called an opioid agonist or

partial agonist) with relatively less potential for abuse. The ideal replacement

opioid should have a less intense or no euphoric effect, should have a longer

pharmacological effect, and should have a withdrawal effect less severe than

that of the abused opioid. Replacement (maintenance) therapy may last

indefinitely, although in many treatment programs the ultimate goal is to

remove the addicts from all drugs and opioids.

10
Antagonist therapy for opioid addiction treats addicts with an opioid antagonist

that blocks binding of opioids to its receptors and thus blocks all effects of

external opioids and, perhaps in some cases, the action of endogenous opioid

peptides. However, this therapy is likely to be successful only for those who are

extremely motivated to stop using opioids or to comply with taking an antagonist

(e.g., physicians who may risk losing their license to practice if they are not off

the drug), In addition, the currently available antagonist agent naltrexone is not

well liked by addicts for several reasons. In some individuals, it may produce

negative mood states. However, these adverse effects are not usually seen in

individuals who have not been dependent on opioids. However, in many cases,

unwillingness to take the antagonist may stem from its therapeutic effects-it

blocks the effects of opioid agonists,

As noted above, in addition to agonist and antagonist therapy, there are drugfree programs. The relapse rates for addicts who enter these programs are

very high, but for small percentages who remain in TCs for 6 months or more,

the outcome is generally quite positive (Vaillant 1992).

OPIOID AGONIST THERAPY

Currently, the only Food and Drug Administration (FDA)-approved

pharmacotherapeutic opioid agonist for drug dependence is methadone

maintenance with counseling. Methadone, given orally once a day to a

tolerant individual, has no or little euphoric effect. Its pharmacological effect

lasts for about 24 hours (thus, need for methadone arises about every 24

hours), and it has less severe though longer lasting withdrawal symptoms

than heroin.

Methadone has been found to be an effective treatment in reducing the use

of illicit opioids that are generally administered through an intravenous (IV)

route. Since IV use and sharing of injection equipment have been associated

with the spread of human immunodeficiency virus (HIV) infection, reduction in

heroin IV use indirectly reduces the risk of HIV infection. Although a decrease

in heroin use is seen within days after methadone is started, in opioid

maintenance with methadone treatment, patients must be stabilized on

methadone for a certain length of time before they can draw maximum benefits

from the treatment. Compared with drug-free programs, considerably higher

retention rates are seen in methadone treatment.

It must be mentioned here that by FDA regulation, methadone maintenance

treatment must include other services such as counseling in addition to the

administration of oral methadone. Hence, there are nonpharmacological

aspects of methadone maintenance treatment. These additional services aid

1 1
addicts, for example, after they have stabilized to the point of ceasing to

participate in crime-related activities, improving social and family relationships,

and remaining in rehabilitation. The quality and quantity of these services can

powerfully affect the results of treatment. Although research has shown that

doses of methadone above 60 mg are more effective than lower doses in

reducing heroin use, there are substantial variations in the methadone dose

(10 mg per day to as much as 100 mg per day) administered in different clinics

as well as in the quality and quantity of nonpharmacological services. Hence,

success rates in reducing IV heroin use vary greatly from one clinic to another

(Ball and Ross 1991; D’Aunno and Vaughn 1992). On the average, over a

1-month period, on a 10-mg daily dose, four of five addicts continue using

heroin; on a 20 to 40 mg per day dose, about half the addicts still use heroin;

on a 40 to 60 mg per day dose, only one of five addicts will use heroin; and on

more than 60 mg per day doses, fewer than one in five addicts continue to use

heroin, provided other services are of high quality.

However, methadone treatment is not without problems. Methadone has a

protracted withdrawal, and, therefore, it is difficult to withdraw from methadone.

It follows that it would be desirable to have an alternative opioid agonist that

induces less severe physical dependence and from which it is easier to

withdraw. Methadone is a full agonist, and fatal accidental overdoses in

unintended users (e.g., nontolerant drug users, children) have been reported.

A treatment agent with less toxicity would be an advantage. Methadone must

be used every day, which can be costly and time-consuming and hinders

rehabilitation; alternatively, addicts must be allowed take-home doses.

Take-home privileges have resulted in diversion of methadone into illicit

markets and, according to isolated reported cases, in the creation of methadone

addicts. Hence, an agent that has longer pharmacological action (e.g., can be

used twice or thrice a week rather than every day and is less susceptible to

diversion) would be an advance. In addition, in certain neighborhoods and

communities, methadone is not well accepted and has been perceived as a

stigma. Alternative treatments that are more acceptable to such communities

would be an advantage.

REFERENCES

American Psychiatric Association. Diagnostic and Statistical Manual of Mental

Disorders. 3d ed., revised. Washington, DC: American Psychiatric

Association, 1987.

Ball, J.C., and Ross, A. The Effectiveness of Methadone Maintenance

Treatment. New York: Springer-Verlag, 1991.

D’Aunno, T., and Vaughn, T.E. Variations in methadone treatment practices

results from a national study. JAMA 267:253-258, 1992.

12
Goldstein, A.; Aronow, L.; and Kalman, S.M. Principles of Drug Action: The

Basis of Pharmacology. New York: Wiley, 1974. 854 pp.

Jaffe, J.H. Current concepts of addiction. In: O’Brien, C. P., ed. Addictive

States. New York: Raven Press, 1992. pp. 1-21.

Methadone maintenance criteria. Federal Register 54(40):8954-8971, 1989.

Vaillant, G.E. Is there a natural history of addiction? In: O’Brien, C.P., ed.

Addictive States. New York: Raven Press, 1992. pp. 1-21.

World Health Organization. 1990 draft of chapter V: Mental and behavioral

disorders. Clinical descriptions and diagnostic guidelines. International

Classification of Diseases. 10th rev. Geneva: World Health Organization,

1990.

AUTHORS

Frank J. Vocci, Ph.D.

Deputy Director

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

Jerome H. Jaffe, M.D.

Deputy Director

Office of Treatment Improvement

Rockwall II, 10th floor

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

13
Background and Design of a Controlled

Clinical Trial (ARC 090) for the

Treatment of Opioid Dependence

Rolley E. Johnson and Paul J. Fudala

INTRODUCTION

The initial clinical abuse liability study of buprenorphine was reported by Jasinski

and coworkers (1978). They noted that acute single doses of buprenorphine

produced morphine-like subjective, physiologic, and behavioral effects. They

also found buprenorphine to be acceptable to the addict population and to block

the effects of subcutaneously administered morphine. Buprenorphine appeared

to have a long duration of action similar to methadone but, unlike methadone,

was associated with a limited physiologic withdrawal syndrome. In the same

report, the chronic subcutaneous administration of 8 mg/day of buprenorphine

was equivalent to 60 mg/day of orally given methadone for subject-reported

“liking.” A later study (Mello and Mendelson 1980) provided additional data

regarding the potential efficacy of buprenorphine by showing that it suppressed

the rate of heroin self-administration by individuals participating in a clinical

laboratory study.

The relative ineffectiveness by the oral route of administration (Jasinski et al.

1982) led to studies using sublingual buprenorphine. These investigations

demonstrated that sublingually given buprenorphine was two-thirds as potent

as when administered subcutaneously (Jasinski et al. 1989). Subsequent

studies focused on various dose-induction procedures and the appropriate

dose levels for the treatment of street opioid- and methadone-dependent

individuals (Jasinski et al. 1983; Reisinger 1985; Seow et al. 1986; Bickel

et al. 1988a; Kosten and Kleber 1988).

Bickel and colleagues (1988a) reported that sublingual buprenorphine, 2 mg/day.

was significantly less effective than 30 mg of orally administered methadone in

attenuating the effects of a hydromorphone challenge. The same authors later

reported that the opioid-blocking activity of buprenorphine was dose related up to

8 mg/day (Bickel et al. 1988b), with little apparent increase in benefit when the

dosage was increased to 16 mg/day.

14
Still to be determined were appropriate induction and dosing schedules for a

clinical comparison of buprenorphine with methadone. Thus, an inpatient trial

was conducted to address these therapeutic issues. Results from this study

indicated that a rapid 3-day dose-induction procedure was both effective and

acceptable to study participants (Johnson et al. 1989). It was also concluded

that daily dosing was probably more appropriate than alternate-day dosing

(Fudala et al. 1990).

The present study was designed to meet Food and Drug Administration

regulatory requirements for a well-designed, well-controlled clinical trial that

could be used in support of a New Drug Application for buprenorphine. To this

end, the investigators attempted to control or account for those aspects of the

study that could confound the data analyses or interpretation (Hargreaves

1983) including issues such as choosing appropriate design and outcome

measures, subject characteristics, attrition, blinding, and others. This chapter

describes the background and design of a controlled clinical trial comparing the

efficacy of buprenorphine and methadone for the short-term maintenance and

detoxification of opioid addicts.

DESIGN

Patients

Inclusion criteria included the following:

1.

2.

3.

4.

5.

6.

7.

Male or female volunteers seeking treatment for opioid dependence

Age 21 to 50 years

Length of present addiction of at least 4 months

At least two or more episodes of heroin use per day

Daily value of heroin use of $50 or greater

A rating of 4 or greater on a self-reported level of withdrawal scale 12

hours after the last heroin dose (0=no withdrawal, 9=worst withdrawal

ever experienced)

Three consecutively collected daily urines, at least two of which were

positive for opioids but negative for methadone

15
Exclusion criteria included the following:

1. Any acute or chronic medical or psychiatric condition that may have

compromised an individual’s ability to complete the study

2. A score of 7 or higher on the interviewer severity rating of need for

psychiatric/psychological treatment on the Addiction Severity Index (ASI)

3. Clinically significant abnormalities in laboratory values

4. Alanine or aspartate aminotransferase levels greater than 99 units/L on

admission

Individuals were recruited through a contract service that identified potential

patients from treatment, general medical, and other facilities having contact

with chronic drug abusers. This service used the Shipley Institute of Living

Scale and the Hopkins Symptom Checklist 90 (Revised) to ensure that

prospective study participants could read and understand both the informed

consent and study questionnaires and also as aids in identifying individuals

who might not be qualified for the study. The study was conducted under

protocol 090 at the Addiction Research Center of the Intramural Division of the

National Institute on Drug Abuse (NIDA), Baltimore, MD, using its outpatient

facilities. Individuals were enrolled in the trial between September 1988 and

November 1989.

Each patient gave informed consent for participation in the study. The consent

forms and experimental procedures were approved by the local institutional

review board in accordance with the U.S. Department of Health and Human

Services guidelines for the protection of human subjects.

Methods

The study was conducted using a double-blind, double-dummy (both an oral

and sublingual dosage form given), parallel groups design. One dosage form

contained the assigned treatment; the other was a matching placebo. The

three treatment groups were:

1. Buprenorphine, 8 mg/day sublingually (n=53)

2. Methadone 20 mg/day orally (n=55)

3. Methadone 60 mg/day orally (n=54)

The 20 mg/day dosage was chosen since one-tenth of the patients in

methadone clinics were treated during the initial 3 months and longer with

16
this or a lesser dose (U.S. Department of Health and Human Services 1984;

Allison et al. 1985). Also, it has been reported that 31 percent of patients

entering methadone treatment can be successfully maintained on a dose of

20 mg/day or less for 4 weeks (Peachey and Lei 1988). The 60 mg/day dosage

was chosen because it was reported as the approximate median daily dosage

used in maintenance therapy (U.S. Department of Health and Human Services

1984) and one that the authors hypothesized would give results significantly

better than those obtained from the 20 mg/day group. The 8 mg/day dosage

of buprenorphine was selected based on previous reports indicating possible

efficacy (Johnson et al. 1989; Fudala et al. 1990) and effects comparable to

those seen with 40 to 60 mg/day of methadone (Jasinski et al. 1978). The

working hypothesis of the study was that buprenorphine 8 mg/day and

methadone 60 mg/day would be more effective than methadone 20 mg/day

and that buprenorphine would be at least 80 percent as effective as methadone

60 mg/day.

The dose-induction procedure is shown in table 1. Patients were subsequently

continued on their maintenance dosage through study day 120.

The study consisted of 120 days of induction/maintenance followed by 49

days of gradual dosage reduction and 11 days of placebo dosing. Patients

who wished to voluntarily terminate their participation in the study or who were

administratively discharged were given a 21-day methadone detoxification.

For the purposes of data analysis, the study was divided into a 17-week

maintenance phase (days 1 through 119) and an 8-week detoxification phase

(days 120 through 175) since the detoxification phase was considered to begin

with the last maintenance dose. The gradual detoxification was carried out by

decreasing each treatment group’s dosage by the same percentage for a given

week of the study. Although the study was designed to be carried out over 175

days (25 weeks), patient participation and data collection were extended to a

total of 180 days to parallel existing Federal methadone regulations for longterm detoxification.

TABLE 1. ARC 090 trial: dose-induction procedure

Study Day

Drug/Dosage 12345678 9 10

Buprenorphine 8 mg 2 4 8 8 8 8 8 8 8 8

Methadone 60 mg 20 30 40 50 60 60 60 60 60 60

Methadone 20 mg 20 30 30 30 30 25 25 25 25 20

17
Stratification

Patients were stratified into treatment groups by the following criteria:

1. Age (21 to 35 and 36 to 50 years).

2. Gender

3. Clinical Institute Narcotic Assessment scores (less than 30 and greater

than or equal to 30) (Peachey and Lei 1988). These scores reflect the

results of a naloxone challenge test that was given to all patients

immediately prior to their receiving the first dose of study medication.

Each stratification factor had two levels for a total of eight strata. Treatment

assignment was performed randomly for each stratum using a permuted block

design with possible block sizes of three, six, or nine.

The naloxone challenge test was used as a stratification variable to ensure

approximately equivalent levels of physical dependence between groups.

Age was used since various authors have shown differences in relapse and

retention rates based on a patient’s age (Richman 1966; Babst et al. 1971;

Brown et al. 1973). Gender differences have been reported to affect retention

of patients in methadone maintenance (Hser et al. 1991) and therapeutic

community treatment programs (Sansone 1980). Also, since the present study

incorporated fixed-dosage regimens, potential pharmacokinetic differences due

to gender were controlled by stratification.

Clinic Milieu

Thirty to sixty minutes of individual counseling per week, using a relapse

prevention model, was offered but not required. Medical safety was evaluated

using hematology and blood chemistry panels and urinalyses collected on

study days 30, 60, 90, 120, and 180. Vital signs were recorded every 2 weeks,

and urine pregnancy tests were obtained every 2 months. Patient case report

forms and medical records were maintained for each participant. Observed

urine samples were collected three times weekly on Monday, Wednesday,

and Friday. To promote patients’ compliance with the urine collection process,

individuals were required to submit a sample on the day(s) following a missed,

scheduled collection. However, because of potential carryover and other

confounds, these samples were not analyzed. Level 1 to level 2 clinical

services (Childress et al. 1991) were provided to all patients.

18
Treatment compliance was maximized by requiring participants to come to

the clinic daily to receive medication. Individuals who missed 3 consecutive

days of medication were dropped from the study, with their third missed day

considered to be the last day of study participation. Every effort was made

to retain individuals in the study. For example, whenever possible, medications

were delivered to and data collected from patients who were incarcerated in the

Baltimore metropolitan area. The last day of study participation for individuals

administratively discharged or those who voluntarily terminated from the study

was their actual discharge or termination date.

One, zero, and three patients, randomized to the buprenorphine and

methadone 20 and 60 mg/day groups, respectively, had their dosages halved

due to an inability to tolerate them. Since this was a fixed-dosage protocol,

these patients were considered treatment failures effective on the first day of

dosage adjustment, although data collection continued. Study staff members

(except pharmacy personnel) were blind to this provision of the protocol.

Primary Dependent Variables

Three primary dependent variables were identified a priori:

1. Patient retention time in the study

2. Monday, Wednesday, and Friday urine samples negative for opioids

3. Failure to maintain drug abstinence as assessed by two consecutive

Monday urine samples positive for opioids following 4 weeks of treatment

The criterion for the last variable was chosen to give patients time to stabilize

in treatment and to account for the probability that patients would more likely

challenge the pharmacologic blockade early in treatment. Monday urine

samples were selected since it was felt that patients were more likely to use

(or use more) illicit opioids on weekends. A 1 -week interval between samples

was chosen so that a positive result would not be due to a previous sample.

Secondary Dependent Variables

Collected within the first 7 study days were results from the following:

1. Buss-Durkee Hostility Scale

2. Diagnostic Interview Schedule

19
3.

4.

5.

6.

7.

8.

9.

Early Experience Questionnaire

Elliot Huizinga Lifetime Events Survey

Eysenck Impulsivity, Venturesomeness, and Empathy Questionnaire

Eysenck Personality Questionnaire

Hopkins Symptom Checklist 90 (Revised)

Personality Diagnostic Questionnaire

ASI (also obtained at study completion or termination and 3, 6, and 12

months thereafter)

The following patient-reported data were collected daily:

1. An adjective checklist (interval scale from 0 to 9) assessing opioid

withdrawal symptoms, with additional items measuring urge and need for

an opioid, frequent urination, and “hooked on” and “liking” for the study

medication

2. A structured questionnaire (true/false) assessing opioid withdrawal

symptoms

Collected three times weekly were urine samples assayed for barbiturates,

benzodiazepines, cocaine metabolite, methadone, and phencyclidine.

Data collected biweekly (patient reported) included:

1. A visual analog scale assessing “want” and “need” for an opioid and

cocaine

2. A 14-item medication adverse effects questionnaire

3. Beck Depression Inventory

Collected at 30, 60, 90, and 120 days and at termination were:

1. Hematology and blood chemistry panels

2 . Urinalyses

3. Vital signs

20
Urine Toxicology

Urine samples were assayed in triplicate using appropriate positive and

negative controls, once with radioimmunoassay (Abuscreen; Roche

Diagnostic Systems Inc., Montclair, NJ) and twice with enzyme-multiplied

immunoassay technique (EMIT; Syva Corporation, Palo Alto, CA). A sample

was considered to be positive if the amount of analyte in the sample was

greater than a predetermined cutoff value (e.g., 300 ng/mL for opioids).

If a sample tested negative at least twice out of the three assays, it was

considered negative; otherwise, it was considered positive.

Study Medications

Buprenorphine hydrochloride was obtained from Reckitt and Colman (Hull,

England) through NIDA’s Research Technology Branch (Rockville, MD). Drug

solutions were aseptically prepared in 30 percent ethanol (vol/vol) and stored

at room temperature. All solutions were administered sublingually in a volume

of 1 mL using Ped-Pod oral dispensers (SoloPak Laboratories, Franklin Park,

IL). Buprenorphine solutions have been shown to be stable in these dispensers

for at least 3 months. To maximize the amount of buprenorphine absorbed

from the sublingual mucosa, all patients were instructed to refrain from speaking

and to hold the solution under the tongue for 10 minutes. Methadone HCI

(methadone hydrochloride oral concentrate USP, 10 mg/mL) and cherry flavor

concentrate (Mallinckrodt Inc., St. Louis, MO) were used. A methadone HCI,

2 mg/mL solution was prepared from the concentrate and distilled water.

Final methadone dosages were prepared to a volume of 30 mL using this

solution in a vehicle of cherry flavor concentrate:water (1:4) containing

denatonium benzoate (Bitrex; J.H. Walker and Co., Inc., Mt. Vernon, NY),

0.2 ng/mL, to mask the flavor of the solutions.

SUMMARY

This study represents the largest clinical trial reported to date that demonstrated

the efficacy of buprenorphine for opioid dependence treatment (Johnson et al.

1992). Although the study design was adequate to demonstrate differences

between treatment groups, there has not been a consensus regarding the most

appropriate method for analyzing various outcome measures of this and similar

studies. To present a comprehensive review of these methods, other chapters

in this monograph focus on various analytical techniques for assessing one of

these measures-urine toxicology screens-for illicit opioids.

21
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Abuse Treatment Research Monograph Series. DHHS Pub. No. (ADM)85-

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Public Health Service, Alcohol, Drug Abuse and Mental Health

Administration, 1985.

Babst, D.V.; Chambers, C.D.; and Warner, A. Patient characteristics associated

with retention in a methadone maintenance program. Br J Addict 66:195-204,

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Bickel, W.K.; Stitzer, M.L.; Bigelow, G.E.; Liebson, I.A.; Jasinski, D.R.; and

Johnson, R.E. A clinical trial with buprenorphine: Comparison with

methadone in the detoxification of heroin addicts. Clin Pharmacol Ther

43:72-78, 1988a.

Bickel, W.K.; Stitzer, M.L.; Bigelow, G.E.; Liebson, I.A.; Jasinski, D.R.; and

Johnson, R.E. Buprenorphine: Dose-related blockade of opioid challenge

effects in opioid dependent humans. J Pharmacol Exp Ther 247:47-53,

1988b.

Brown, B.S.; DuPont, R.L.; Bass, U.F. III; Brewster, G.W.; Glendinning, S.T.;

Kozel, N.J.; and Meyers, M.B. Impact of a large-scale narcotics treatment

program. A six month experience. Int J Addict 8:49-57, 1973.

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minimum conditions necessary for methadone maintenance to reduce

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C.G.; and Schuster, C.R., eds. Improving Drug Abuse Treatment. National

Institute on Drug Abuse Research Monograph 106. DHHS Pub. No.

(ADM)91-1754. Washington, DC: Supt. of Docs., U.S. Govt. Print. Off., 1991.

pp. 167-177.

Fudala, P.J.; Jaffe, J.H.; Dax, E.M.; and Johnson, R.E. Use of buprenorphine in

the treatment of opioid addiction. II. Physiologic and behavioral effects of

daily and alternate-day administration and abrupt withdrawal. Clin Pharmacol

Ther 47:525-534, 1990.

Hargreaves, W.A. Methadone dosage and duration for maintenance treatment.

In: Cooper, J.R.; Altman, F.; Brown, B.S.; and Czechowicz, D., eds.

Research on the Treatment of Narcotic Addiction. State of the Art. National

Institute on Drug Abuse Treatment Research Monograph Series. DHHS

Pub. No. (ADM)83-1281. Rockville, MD: U.S. Department of Health and

Human Services, U.S. Public Health Service, Alcohol. Drug Abuse, and

Mental Health Administration, 1983. pp. 19-79.

Hser, Y.; Anglin, M.D.; and Liu, Y. A survival analysis of gender and ethnic

differences in responsiveness to methadone maintenance treatment. Int J

Addict 25:1295-1315. 1991.

22
Jasinski, D.R.; Fudala, P.J.; and Johnson, R.E. Sublingual versus

subcutaneous buprenorphine in opiate abusers. Clin Pharmacol Ther 45:

513-519, 1989.

Jasinski, D.R.; Haertzen, C.A.; Henningfield, J.E.; Johnson, R.E.; Makhzoumi,

H.M.; and Miyasato, K. Progress report of the NIDA Addiction Research

Center. In: Harris, L.S., ed. Problems of Drug Dependence, 1981:

Proceedings of the 43rd Annual Scientific Meeting, The Committee on

Problems of Drug Dependence, Inc. National Institute on Drug Abuse

Research Monograph 41. Washington, DC: Supt. of Docs., U.S. Govt.

Print. Off., 1982. pp. 42-52.

Jasinski, D.R.; Henningfield, J.E.; Hickey, J.E.; and Johnson, R.E. Progress

report of the NIDA Addiction Research Center, Baltimore, Maryland, 1982.

In: Harris, L.S., ed. Problems of Drug Dependence, 1982: Proceedings of

the 44th Annual Scientific Meeting, The Committee on Problems of Drug

Dependence, Inc. National Institute on Drug Abuse Research Monograph 43.

DHHS Pub. No. (ADM)83-1264. Washington, DC: Supt. of Docs., U.S. Govt.

Print. Off., 1983. pp. 92-98.

Jasinski, D.R.; Pevnick, J.S.; and Griffith, J.D. Human pharmacology and abuse

potential of the analgesic buprenorphine. Arch Gen Psychiatry 35:501-516,

1978.

Johnson, R.E.; Cone, E.J.; Henningfield, J.E.; and Fudala, P.J. Use of

buprenorphine in the treatment of opiate addiction. I: Physiologic and

behavioral effects during a rapid dose induction. Clin Pharmacol Ther

46:335-343, 1989.

Johnson, R.E.; Jaffe, J.H.; and Fudala, P.J. A controlled trial of buprenorphine

treatment for opioid dependence. JAMA 267:2750-2755, 1992.

Kosten, T.R., and Kleber, H.D. Buprenorphine detoxification from opioid

dependence: A pilot study. Life Sci 42:635-641, 1988.

Mello, N.K., and Mendelson, J.H. Buprenorphine suppresses heroin use by

heroin addicts. Science 207:657-659, 1980.

Peachey, J.E., and Lei, H. Assessment of opioid dependence with naloxone.

Br J Addict 83:193-201, 1988.

Reisinger, M. Buprenorphine as new treatment for heroin dependence. Drug

Alcohol Depend 16:257-262, 1985.

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11:107-115, 1966.

Sansone, J. Retention patterns in a therapeutic community for the treatment of

drug abuse. Int J Addict 15:711-736, 1980.

Seow, S.S.W.; Quigley, A.J.; Ilett, K.F.; Dusci, L.J.; Swensen, G.; HarrisonStewart, A.; and Rappaport, L. Buprenorphine: A new maintenance opiate?

Med J Australia 144:407-411, 1986.

23
U.S. Department of Health and Human Services. National Summary of Narcotic

Treatment Programs. Annual Report for Treatment Programs Using

Methadone. Washington, DC: Supt. of Docs., U.S. Govt. Print. Off., 1984.

ACKNOWLEDGMENTS

This work was supported through the NIDA intramural research budget. The

authors acknowledge Jean Fralich, Louise Glezen, and John Hickey for

medical monitoring and coordinating the study; Ed Bunker, Charles Collins,

Jose deBorja, Nancy Kreiter, Ivan Montoya, and Renea Siebold for data entry,

computer programing, and statistical analysis; Ed Brown, Tommy Calloway,

Denise Dickerson, Marge Ewell, and Ramona Parker for patient recruitment;

C. Dan Baker and Faye Hodges for patient counseling; and Anna Dorbert and

Lillian Morgan for nursing services.

AUTHORS

Rolley E. Johnson, Pharm.D.

Associate Professor

Department of Psychiatry and Behavioral Sciences

The Johns Hopkins School of Medicine

Building G, Room 2725

5510 Nathan Shock Drive

Baltimore, MD 21224

Paul J. Fudala, Ph.D.

Assistant Professor

Department of Psychiatry

University of Pennsylvania School of Medicine and the Department of Veterans

Affairs Medical Center

Building 15

University and Woodland Avenues

Philadelphia, PA 19104

24
Clinical Endpoints: Discussion

Session

Ram B. Jain

Discussants: John Hyde, Charles Gorodetzky, Richard Stein, and Curtis

Wright

The aim of this discussion session was to obtain the opinion of the U.S.

Food and Drug Administration (FDA) about what kind of endpoints would be

adequate and/or appropriate in clinical trials for treatment of drug dependence,

what statistical methods should be used to analyze the data generated from

these trials, and in general, what strategy should be used to design these trials.

Drs. Hyde, Stein, and Wright represented FDA, and Dr. Gorodetzky presented

the pharmaceutical industry’s viewpoint because FDA policy might affect its

ability to conduct clinical trials.

Dr. Wright reminded that although most funded research is exploratory in

nature, generating new and exciting information on the cutting edge of science,

most of the drug approval work at FDA is confirmatory in nature, calling for

regulatory decisions to approve or not approve drugs. As a consequence,

results obtained by applying a new mathematical technique should be backed

up or linked with results obtained by a mathematical technique that is known

to work. Drug approval is easy when information about a new drug is coherent

and robust and there is a large effect size. The results obtained in large phase

III trials—generally used to support a new drug application (NDA)—should be

in coherence with the results obtained from the earlier phase I and II trials in

selected and general human populations and from preclinical work on animals;

they should get the same answers in all those places. The conclusions

obtained from analysis of data should be robust; that is, they should not be

dependent on a specific experimental design, a specific method of analysis,

or the specific way a trial may have been conducted. Different trials, probably

using different designs, should lead to the same conclusions, This is what

Dr. Stein called clinical robustness as opposed to statistical robustness. The

effect size should be relatively large.

25
The results of the pivotal trials should not depend on a set of assumptions

made at any stage of development. Outcome variables (endpoints) selected

for the pivotal trials should tap several different kinds of domains. Subjective

self-reports (e.g., “How are you doing today?”) should be linked or obtained in

parallel with observer rating by a clinical staff member or physician about,

for example, how the addict was doing that day. Physiologic measures or

responses—for example, urine screens, hair analysis, naloxone challenge

scores—should be obtained along with behavioral measures such as retention

rates. Common or similar results across different domains sampled strengthen

an NDA.

FDA’s Pilot Drug Evaluation Division would permit four primary variables

without penalizing for multiplicity. An approval may become difficult if effect is

shown for only one variable in one population in one study only. The results

obtained by analyzing a data set validated by FDA’s Division of Scientific

Investigations using a specific method (of analysis) are cross-validated by

analyzing data using some other techniques to see whether the findings are

robust. Implicit assumptions built into data collection, reduction, and analysis

are evaluated. Knowledge of what took place at each step along the way—

from preclinical work to analysis of phase III trials—is helpful. Trial designs

that not only meet the requirements of a particular analytical technique to be

used but also are robust toward dropouts, violation of protocol assumptions,

and alternative analytical techniques are preferable. This is so because trials

designed to prove efficacy may also be looked at to try to determine the dose,

to evaluate adverse reactions, or to develop specific instructions for use for

subpopulations. It is also important to look at what information may have been

thrown away and what information may be so confounded that dose, duration

of treatment, patient acceptability, specific adverse events, and management

of patient dropouts are so distorted that the trial cannot be used to make a

regulatory decision.

Dr. Stein believed it important to evaluate the social impact of the proposed

drug in these populations. How healthy and how productive the patients may

be after the treatment is probably a primary variable for these populations. The

endpoints should be reliable and quantifiable. Simple surrogate measures such

as how frequently the drug is abused, what is the abuse pattern, and how much

and what kind of drug is being abused are important. An acceptable analysis

should be able to identify how each patient did during the treatment and what

his or her contribution is to the overall analysis.

Dr. Gorodetzky commented about the use of four primary variables. The

number of primary variables to be used will depend on the kind of experiment

designed and whether it is aimed at the consumer, at the science, or at

26
medicine. Some kind of compromise is possible. A clinical trial is an

experiment in which one has to think very specifically about the objectives

and the operational manner in which one is going to attempt to reach those

objectives. One may not want to do certain things in a given situation that

might be interesting to do in another context. It is not as simple as choosing

one variable or four variables; the question is how some very practical

questions can be answered and how specific objectives can be drawn up for

clinical trials.

The end product of an approved drug is a package insert aimed at the

users-the practicing physicians and other scientists. The package insert

communicates what should be expected from the approved drug. As

Dr. Wright put it, what should be communicated to these users is fairly basic

practical data: For example, is the patient going to be arrested less often?

Is the patient going to be using drugs less? Is the patient going to come back

to the clinic? If a package insert communicates information that is too complex,

it would not be understandable to the users of a package insert.

As Dr. Wright pointed out, combination variables are good at supporting a

fairly robust statistical outcome, but they can make it extremely difficult to go

back to the original data for dose selection, to develop instructions for use for

subpopulations, and to establish relationships between adverse events and

treatment drugs.

There was some discussion about the retention rates in these trials. How

should this variable be used? What does this variable mean? Dr. Vocci

wanted to use this variable as an outcome measure not only because it is

important for the analysis, but also because, if a treatment works for only a

subpopulation, there is an interest in knowing the characteristics of that

subpopulation. This variable might tell who is going to be a possible treatment

success. Retention is important because, before patients can benefit from the

treatment and, thus, start changing their behavior (other than drug-taking

behavior), they must stay in the treatment for a certain length of time. This

reflects on the effectiveness of a treatment program vs. the effectiveness of a

drug. According to Dr. Gorodetzky, retention is a complex variable and may

have more practical consequences than some of the other outcome variables.

Because treatment milieu differs substantially from one clinic to another, the

largest treatment by investigator (clinic) interaction is likely to be discovered

for retention in multicenter trials. People may drop out of these trials for

different reasons: because of a 4-hour questionnaire they are asked to

complete on the last day of the treatment; because the treatment failed for

them; or because of how they get paid, how much they are paid, and when.

Dropouts modify treatment effects in these trials in unknown ways.

27
AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

28
Design of Clinical Trials for Treatment

of Opiate Dependence: What Is

Missing?

Ram B. Jain

INTRODUCTION

A typical trial to evaluate the safety and efficacy of a new pharmacotherapy

for the treatment of drug dependence, including opiate dependence, would

be double blind and would use one or more doses of the new pharmacological

agent as well as a placebo and/or an active control as the alternative treatment

arm. The primary outcome variable of interest will be the frequency and/or

the amount of the addicting/abused opiates used by the subjects in the trial

in different treatment arms. The only practical way to determine either the

frequency or the amount of the addicting/abused opiates used by the addicts

would be through self-reports. However, these self-reports are not likely to be

very reliable. Consequently, the addicts are asked to provide urine samples

as specified in the protocol. These urine samples are assayed to determine

the presence and/or the amount of the addicting/abused opiates.

T1 and T2 are the two consecutive time points (figure 1) at which a subject

provides urine samples for testing. If episodes A, B, and C are three

independent episodes of opiate abuse, then A will not be detected at either

T1 or T2, B will be detected at T, only, and C will be detected at both T, and

T2 since the amount of opiate abused at these episodes was different, and as

such the duration for which opiates stay in the urine will be different. To detect

episode A or to avoid underestimation of the frequency of opiate abuse, the

urine samples should have been collected and assayed earlier; in other

words, to avoid underestimation, the urine samples should be collected as

frequently as possible. To avoid episode C being detected twice or to avoid

overestimation of the frequency of opiate abuse, the urine samples should

be collected as infrequently as possible. The phenomenon of two or more

consecutive samples detecting the same episode of opiate abuse is called

the carryover from one positive sample to another positive sample. There

are substantial variations in drug-seeking behavior from one addict to another:

29
Time at Which Urine Samples Are Collected

FIGURE 1. Detection of drug abuse by urine assays

Some abuse large amounts in relatively few episodes; some use small amounts

in relatively large numbers of episodes; some abuse drugs during weekends

only; and some use them every day. For this reason, it is difficult to determine

whether two or more consecutive positive urine samples represent one or more

episodes of drug abuse or, in other words, whether there is a carryover. Also,

since the estimation of carryover is difficult, carryover or overestimation rather

than underestimation of the frequency of opiate abuse is more of a concern.

However, complete elimination of the probability of carryover may not be

achievable. Hence, it is probably best to design the trials so that the probability

of carryover from one positive urine to another positive urine is minimized

and the probability of detecting an episode of drug abuse is maximized. This

chapter provides suggestions as to how a trial can be designed to achieve this

and what may still be missing.

The issues that reflect on the design of these trials can be studied under the

following titles:

1. Sampling schemes used to obtain urine samples

2. Frequency and timing of the collection of urine samples

3. Qualitative vs. quantitative analysis of urine samples

30
SAMPLING SCHEMES USED TO OBTAIN URINE SAMPLES

In one of the earlier trials conducted to evaluate the safety and efficacy of

LAAM, Ling and colleagues (1976) collected urine samples once a week using

a random time sampling scheme. In a random time sampling scheme, although

the subjects know how many times during a given week they will be asked to

provide their urine samples, they do not know on which days of the week they

will be asked to provide a urine sample. It is randomly decided who will provide

a urine sample on which day of the week. For example, if the protocol calls

for collection of one urine sample per week from each subject and if the urine

samples are to be collected Monday through Friday only, 20 percent of the total

subjects in the study will provide urine samples on Monday, 20 percent of the

total subjects in the study (from the remaining 80 percent of the total subjects)

will provide urine samples on Tuesday, and so on until all the subjects who

have not provided their urine samples by Thursday will be asked to provide their

urine samples on Friday. Consequently, the probability of a subject providing a

urine sample will vary from day to day, ranging from zero to one. Consequently,

this type of sampling scheme is not truly random. In addition, a subject X may

provide a urine sample on Monday of one week and on Friday of the next week,

thus being allowed free drug-seeking behavior for 10 days. On the other hand,

a subject Y may provide a urine sample on Friday of one week and on Monday

of the next week, thus being allowed free drug-seeking behavior for only 2 days.

Thus, a random time sampling scheme has the potential to make alternate

treatment groups incomparable for analysis. As said earlier, this sampling

scheme is not truly random, but for lack of better terminology, it is called a

random time sampling scheme. This type of sampling scheme was earlier

advocated by Goldstein and Brown (1970).

Certain other types of random time sampling schemes are discussed in Harford

and Kleber (1978) and Goldstein and Brown (1970). However, since these

schemes are not in practical use, they will not be discussed further.

According to a report published by the Council on Scientific Affairs (1987),

opiates stay in the urine for about 48 hours. Hence, unless urine samples are

collected at less than 48-hour intervals, carryover is not likely to be a problem.

Consequently, once-a-week, 5-days-a-week random time sampling is not likely

to lead to carryover, but since an addict may be tested as far apart as 10 days,

it certainly will lead to underestimation of the frequency of opiate abuse. But for

twice and thrice a week, 5-days-a-week random time sampling, as can be seen

from tables 1 and 2, the probability of being tested less than 48 hours apart,

that is, on consecutive days, is 54.9 and 45.8 percent, respectively, which is

likely to lead to a serious carryover. The probability of being tested more than

48 hours apart, that is, probability of underestimation, is 18.9 and 13.7 percent,

respectively.

31
TABLE 1. Probabilities of being tested in a twice-a-week, 5-days-a-week

random time testing*

Probability of

Being Tested on

M T W T F

Minimum (Maximum)

Number of Free Number of Free

Drug-Seeking Days Drug-Seeking Days

During the Week During 2 Weeks

X X .1600000 5 5 (8)

X X .1142857 4 4 (7)

X X .0628571 3 3 (6)

X X .0628571 2 2 (5)

X X .1142859 4 4 (7)

X X .0628571 3 3 (6)

X X .0628571 2 2 (5)

X X .0857142 3 3 (6)

X X .0857142 2 2 (5)

X X .1885714 2 2 (5)

*Total probability of being tested on consecutive days=.5485713; probability of

being tested more than 48 hours apart during the same week=.1885713.

Hence, random time sampling could render treatment groups incomparable for

analysis and may result in serious underestimation of the frequency of opiate

abuse and/or a serious carryover from one positive sample to another positive

sample depending on the frequency of sampling.

To further dwell on the merits and demerits of random time sampling, another

type of sampling scheme called fixed time sampling needs to be defined.

In a fixed time sampling scheme, all subjects are asked to provide urine

samples on the same days of the week. In a double-blind, double-dummy

clinical trial to compare the efficacy and safety of 8-mg sublingual doses of

buprenorphine with 20- and 60-mg doses of methadone conducted at the

Addiction Research Center of the National Institute on Drug Abuse (the ARC

090 trial), between September 1988 and May 1990, a fixed time sampling

scheme was used to obtain urine samples three times a week on Mondays,

Wednesdays, and Fridays. Because the urine samples were obtained at least

48 hours apart, the probability of carryover is minimal. According to Dr. Edward

J. Cone (personal communication, July 1991) of the Addiction Research Center,

the mean time to detect (cutoff=300 ng/mL) intramuscular administration of 6

mg of morphine by an enzyme-multiplied immunoassay technique (EMIT)

32
TABLE 2. Probabilities of being tested in a three-times-a-week, 5-days-aweek random time testing*

Probability of Number of Free

Being Tested on Drug-Seeking Days

MTWTF During the Week

Number of Free

Drug-Seeking Days

During 2 Weeks

XX X .1885714

X X X .1487258

X X X .0227026

X X X .1090656

X X X .0151350

X X X .1142857

X X X .1090656

X X X .0151350

X X X .1142857

X X X .1600000

4 4 (6)

3 3 (5)

2 2 (4)

3 3 (5)

2 2 (4)

2 2 (4)

3 3 (5)

2 2 (4)

2 2 (4)

2 2 (4)

 *Total probability of being tested on consecutive days=.457637; probability of

being tested more than 48 hours apart during the same week=.1369883.

assay was 21.82 hours (n=5, SD=5.34). Given that the urine half-life of

morphine is 4 to 6 hours, on the average, up to 96 mg of morphine can be

consumed by an addict during one episode and still result in only one positive

urine if the consecutive urines are collected and assayed at least 48 hours

apart. However, since Friday and Monday samples were collected 72 hours

apart, the potential for underestimation is certainly there, but this is likely to

happen only when opiates are abused on Fridays but not on Saturdays and

Sundays. At worst, the addicts have 3 free days of drug-seeking behavior.

But because everybody has the same number of free days uniformly across

the whole study period, the comparability of different treatment groups is

maintained.

The strongest argument in favor of random time sampling is that the addicts

try to avoid drug abuse detection, and as such, if they know they will be tested,

they will not show up for their scheduled visits. In certain special treatment

situations in which a positive result is associated with certain contingencies,

this might be true, but in a clinical trial environment there is no reason to

expect any such contingencies. As such, the argument to use random time

sampling is merely philosophical, with no advantage and many drawbacks,

including a substantial potential to render the data nonanalyzable. If a protocol

calls for administrative withdrawal after a certain number of positive urines, the

addict may be switched to an alternate, possibly more beneficial treatment

33
rather than being withdrawn, and makeup urines may be collected on days

following a missed visit; these makeup urines may or may not be used in the

analysis, In addition, there are no published data to suggest that such a

practice does occur in a noncontingent treatment environment.

Hence, a fixed time sampling should be the design of choice.

FREQUENCY AND TIMING OF THE COLLECTION OF URINE SAMPLES

When and how frequently the urine samples should be collected depends

on the kinetics of the drug of abuse and the sensitivity of the assay used to

analyze the urine samples. For heroin, with a cutoff of 300 ng/mL, a sample

every 48 hours seems to be the optimal choice, because as pointed out by the

Council on Scientific Affairs (1987), heroin stays in the urine for about 48 hours

provided EMIT-type assays are used. This is likely to minimize the probability

of carryover and maximize the probability of detecting an episode of opiate

abuse.

With a lower cutoff and/or a more sensitive assay such as gas chromatography/

mass spectrometry, the samples may have to be collected and assayed more

infrequently. Otherwise, the probability of carryover may be increased.

However, this may decrease the probability of detecting an episode of drug

abuse.

Also, for shorter acting drugs, the samples may have to be collected more

frequently. For longer acting drugs, they may have to be collected more

infrequently.

The timing of sample collection should be such that the days of heavy use

do not go undetected. For example, to detect use on weekends, it may be

necessary to collect the first sample of the week on Monday.

In summary, the decision of when and how frequently the samples should be

collected should be made by a joint team: a statistician, who should ensure

that the probability of carryover is minimized and the probability of detecting

the drug abuse is maximized to the degree possible; a pharmacologist/

pharmacokineticist, who should ensure that reliable information on the kinetics

of the drug of abuse is available and is provided to the statistician; and a

physician/clinician, who is adequately informed of the pattern of drug abuse and

should be primarily responsible for the timing of sample collection.

34
QUALITATIVE VS. QUALITATIVE ANALYSIS OF URINE SAMPLES

Currently, the clinical trials in the drug abuse area are designed to estimate

the frequency of drug abuse and not the amount of drug abuse. However, a

replacement drug may decrease the frequency of drug abuse, but the addicts

may still be using the same amount of the drug (of abuse), though in a smaller

number of episodes. The amount of drug abuse may be estimated by analyzing

the urine samples quantitatively rather than qualitatively, that is, by estimating

the amount of the drug of abuse in the urine, rather than just the presence or

absence of the drug of abuse. However, a real-life relationship between the

amount of drug present in the urine and the actual amount of drug consumed is

confounded by many factors.

A relationship between the amount of drug present in the urine and the actual

amount of drug consumed may be established in laboratory experiments, and

an inference can be drawn about the amount of drug consumed from the

amount of drug present in the urine. However, a relationship established in the

laboratory is not likely to hold in real-life situations because of the uncertainty of

the timing of the episodes of drug abuse, the variations in the purity of drugs of

abuse with different geographic locations and times, the effect of multiple

episodes of drug abuse on the metabolism of these drugs, the interactions

between multiple drugs of abuse consumed by the addicts in same or different

episodes, the differences in frequency and timing of drugs abused by the

addicts, and so on. And, of course, how accurately this relationship can be

determined will also depend on the accuracy of the quantitative assays used to

analyze urine samples. In addition, instead of urine samples, plasma samples

may be better determinants of this relationship, but once again, this relationship

too will be confounded by the same factors that confound this relationship for

urine samples.

At best, a relationship between the amount of drug present in the urine or

plasma samples and the actual amount of drug abused is very complex and

not easy to capture in real-life situations. However, a joint effort by statisticians,

pharmacokineticists, and physicians/clinicians to model this relationship is likely

to be fruitful.

It must also be mentioned that the estimation of the amount of drug abuse

should not be done in lieu of the estimation of the frequency of drug abuse.

Both should be done simultaneously. Because of the strong relationship

between the frequency of intravenous use and human immunodeficiency

virus infection, it is of paramount importance that the replacement drugs

should decrease the frequency as well as the amount of drug abuse.

35
WHAT IS MISSING?

1. The statistical/pharmacokinetic methods/design to model the relationship

between the amount of drugs present in the urine or plasma samples and

the actual amount of drugs abused is missing.

2. The present methods to estimate the frequency of drug abuse provide, at

best, a lower bound on the frequency of drug abuse because of:

The inability to detect possible multiple episodes of drug abuse during

the time two consecutive urine samples are collected, and

The need to do infrequent sampling to minimize the carryover from one

positive sample to another positive sample.

3. The probability of carryover is not entirely eliminated, and the degree of

carryover is not known. It will be helpful if methods/techniques can be

developed to ascertain whether multiple, consecutive positive samples are

due to one or multiple episodes of drug abuse. This may, for example, be

done by using self-reported episodes of drug abuse during the time

consecutive urine samples are collected.

REFERENCES

Council on Scientific Affairs, Scientific issues in drug testing. JAMA 257:3110-

3114, 1987.

Goldstein, A., and Brown, B.W. Urine testing schedules in methadone

maintenance treatment of heroin addiction. JAMA 214:311-315, 1970.

Harford, R.J., and Kleber, H.D. Comparative validity of random-interval and

fixed-interval urinalysis schedules. Arch Gen Psychiatry 35:356-359, 1978.

Ling, W.; Charuvastra, V.; Kaim, S.C.; and Klett, C.J. Methadyl acetate and

methadone as maintenance treatments for heroin addicts. Arch Gen

Psychiatry 33:709-720, 1976.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

36
Comments on “Design of Clinical Trials

for Treatment of Opiate Dependence:

What is Missing?” by Jain

Sudhir C. Gupta

This chapter discusses the following three important issues in the design of

clinical trials for opiate dependence:

1. Random vs. fixed time sampling scheme for collecting urine samples

2. Frequency and timing for collecting urine samples

3. Estimating the amount of drug abuse in addition to the frequency of drug

abuse

SAMPLING SCHEME FOR COLLECTING URINE SAMPLES

As discussed by Dr. Jain, the main problem with using a random time sampling

scheme is that the methods for analyzing the data obtained using this scheme

may not be available. This means that suitable methods should first be

developed before the analysis of the data can be carried out. As pointed out by

Dr. Jain, this approach is not recommended. The trial should be designed so as

to allow an efficient interpretation of the data. A fixed time censoring scheme is

thus recommended.

The strongest argument in favor of random time sampling is that addicts try to

avoid drug abuse detection. In a fixed time sampling scheme if they know that

they will test positive because of drug abuse, they may not show up for their

scheduled visits. However, Dr. Jain has pointed out that this is not to be

expected in this trial because subjects who are known to be drug addicts do not

have anything to gain by avoiding detection of drug abuse. In a fixed time

sampling scheme all the subjects are required to provide urine samples on each

of the scheduled days. Sometimes it may become necessary to use a random

time sampling scheme if enough resources are not available to handle all the

subjects in one day. If a random time sampling scheme is to be used under

such circumstances, then it should be modified to yield truly random samples as

indicated below.

37
Suppose the protocol calls for collection of two urine samples per week from

each subject. Then there should be an equal probability for a subject to be

tested on any 2 of the 5 days of the week. Let MTh denote that a subject is to

be tested on Monday and Thursday, etc. A subject may be tested on MT, MW,

MTh, MF, TW, TTh, TF, WTh, WF, or ThF, resulting in 10 possibilities as pointed

out by Dr. Jain. A subject should be assigned to one of these 10 possibilities

randomly. This random assignment should be done separately for each week,

and it should not be known to the subjects in advance of their urine collection.

In the case of two urine samples per week, the expected number of free

drug-seeking days is 3.15 using table 1 of Dr. Jain’s chapter. For the above

suggestion the probability is 0.10 for a subject to be tested on any of the 10

possible pairs of days. The expected number of free drug-seeking days is

then 3.0.

A similar method can be used for three urine samples per week, reducing the

expected number of free drug-seeking days to 2.2. The corresponding

expected number is 2.74 from Dr. Jain’s chapter.

FREQUENCY AND TIMING FOR COLLECTING URINE SAMPLES

As pointed out by Dr. Jain, the frequency of collecting urine samples should be

determined so as to minimize the probability of carryover and to maximize the

probability of detecting opiate abuse. As discussed in Gupta (1991), a model

that incorporates subject and carryover effects can be developed using the

approach of Bonney (1987). However, in this approach the subject effects and

carryover effects are confounded, and a separate estimate of carryover effect is

not provided. This does not seem to be a serious limitation.

ESTIMATING THE AMOUNT OF DRUG ABUSE IN ADDITION TO THE

FREQUENCY OF DRUGABUSE

Dr. Jain has clearly discussed the problems associated with estimating the

amount of drug abuse in addition to the frequency of abuse. As pointed out by

Dr. Jain, currently the clinical trials in this area are designed to estimate the

frequency of drug abuse and not the amount of drug abuse. If the addict tests

positive for drug abuse, then it is important to find out the extent to which the

drug was abused. In other words, it is important to know if a replacement

therapy is effective in reducing the total amount of drug abused in addition to

reducing the frequency of drug abuse. A relationship between the amount of

drugs present in the urine and the amount of drug consumed by the addict may

be established in laboratory experiments, from which an estimate of the amount

of drug consumed may be obtained. However, as Dr. Jain has clearly pointed

out, such estimates are confounded by many factors. Therefore, such

38
estimates derived using the results obtained in the laboratory will not be

precise. Under these circumstances it will be best to study the extent rather

than the exact amount of drug abuse. Let us assume, for example, that the

extent of drug abuse is categorized as low, medium, or high.

Let the outcome variable Y be coded as 0 if the assay shows absence of

abused opiates in the urine. Similarly, Y = 1, 2, 3 will be used to denote that

the assay shows the extent of drug abused to be low, medium, and high,

respectively. Since the outcome variable takes more than two distinct values,

an appropriate polytomous logistic regression model can be developed for

comparing the probabilities under different treatments after adjusting for the

effects of covariates. A patient provides repeated observations up to a

maximum of 17 weeks. Since each dose of a treatment drug provides one

observation, a maximum of 51 replications for a treatment can be obtained for

any patient. These observations from the same patient will not be independent.

Thus, conditional probabilities will be used under the polytomous logistic

regression setup.

Suppose that there are ni observations for the ith patient, which are denoted by

Yij, and let Xij = (X1ij, X2ij, . . . , Xpij)' denote the vector of covariates

associated with Yij, i = 1, 2, . . . , m, j = 1, 2, . . . , ni. Let

Following the approach of Bonney (1987) as discussed by Gupta (1991) for the

case of dichotomous outcome variables, the conditional probabilities as defined

above can be modeled by considering Y as covariates. Let

39
The logits for comparison with Y = 0 are thus obtained as given below. The

logits for comparing with other values of Y can be written down in a similar way.

Following Gupta (1991), finally the model can be written as given below.

40
and n denotes the maximum number of repeated observations possible for a

subject, in the present case n = 51.

The parameters of the model are estimated using the method of maximum

likelihood. Note that in practice certain interactions may be needed to be

included in the model.

REFERENCES

Bonney, G.E. Logistic regression for dependent binary observations. Biometrics

43:951-973, 1987.

Gupta, S. “Analysis of Treatment for Drug Dependence Data Using Logistic

Regression,” Paper presented at the Technical Review Committee Meeting

on Statistical Issues in Clinical Trials for Treatment of Drug Dependence,

National institute on Drug Abuse, December 2-3, 1991.

AUTHOR

Sudhir C. Gupta, Ph.D.

Associate Professor

Division of Statistics

Northern Illinois University

DeKalb, IL 60115-2888

41
Rejoinder

Ram B. Jain

In his comments, Dr. Gupta seems to suggest that if subjects can be tested on

any x (2) days of the week in an x (2)-days-a-week random time sampling with

the same probabilities, this sampling scheme can be considered to be truly

random. I am not quite sure if this is essentially true. Once the subject has

been tested on any 2 days during a given week, he or she will have zero

probability of being tested again and will be free to abuse the drugs. If the

sampling must be truly random, he or she should have equal probability of

being tested on any given day of the week on which urine samples are

scheduled to be collected.

In addition, the biggest problem with random time sampling schemes is not

that they are not truly random. Their biggest problem is that in these kinds

of sampling schemes some subjects are tested too soon after their previous

test and some are tested too long after their previous test. This leads to the

problem of carryover and the loss in ability to detect an episode of drug abuse.

Dr. Gupta also suggested in his written comments and during the meeting that

carryover can be incorporated in the model based on a previous positive urine.

Unfortunately, two or more consecutive positive tests do not always indicate a

carryover. An assumption that two or more consecutive positive urines always

indicate a carryover is likely to lead to underestimation of the probability of drug

abuse. However, subjects’ self-reports about the past drug abuse may be used

to make a decision as to whether two or more consecutive positive urines

indicate a carryover.

Dr. Gupta indicates in his comments that the logistic regression model he

proposed can be used to incorporate carryover effect, but subject effect and

carryover effect will be confounded and a separate estimate of carryover effect

will not be available. I believe this is a serious limitation. Dr. Gupta does not

agree.

In the absence of methodology to exactly estimate the amount of drug abuse,

Dr. Gupta suggests a logistic regression model to estimate the extent of drug

abuse categorized as low, medium, or high. This certainly would be an idea

42
worth pursuing. However, to depend on the assays to categorize as low,

medium, or high drug use will be somewhat unreliable because the amount of

drug present in the urine at the time of testing not only depends on the amount

of drug consumed but also on the time the drug was consumed since the last

urine sample was collected. The timing of the episodes of drug abuse since the

last urine sample was collected is not likely to be known with much accuracy.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

43
Summary of Discussion: “Design of

Clinical Trials for Treatment of Opiate

Dependence: What Is Missing?”

Ram B. Jain

Dr. Murphy expressed the concern that by asking the subjects to come to

the clinic to provide urine specimens three times a week in a fixed time

sampling, we are creating a compliance problem. Even if there are no

negative contingencies associated with the positive urines, certain subjects

will not enroll because they will have to provide urine specimens three times

a week. Retention rates might be adversely affected in a three-times-a-week

fixed time sampling. I pointed out that if the subjects are asked to come to the

clinic three times a week, the problem will be the same whether it is a fixed time

or random time sampling. If Dr. Murphy’s suggestion was to ask them to come

to the clinic once a week, we would be knowingly collecting fewer data than are

needed to estimate treatment effects. A lot of episodes will go undetected in

once-a-week sampling. This will defeat the purpose of the clinical trials, which

is to estimate the treatment effect from several different treatments and

compare them for efficacy.

As pointed out by Dr. Vocci, the primary purpose of a clinical trial is to

evaluate the pharmacological effect of the treatment in a natural setting

rather than to manipulate dropout rates and/or drug abuse rates by introducing

negative contingencies into the trial, and there were none in the ARC 090

trial. In addition, as Dr. Johnson pointed out, the subjects were asked to

hold medication under the tongue for 10 minutes in this trial; this alone would

create some compliance problems. Since the subjects come to the clinic

every day for their medication and other procedures, asking them to provide

urine specimens for 3 of these 7 days should create no additional compliance

problems.

Dr. Jack C. Lee expressed concern about differences (periodicity) in missed

visit rates, percent positive rates, etc., on the different days (Monday vs.

Wednesday vs. Friday) the urine specimens were obtained, as was seen in

Follmann and colleagues’ chapter. Dr. Lee suggested that, in place of

44
collecting the samples a fixed number of times on fixed days of the week, a

random scheme may be adopted so that the expected number of tests during a

week may be fixed (e.g., three), but the samples may be collected on different

days of the week and a different number of times during different weeks. This

may help smooth out the periodic (cyclic) effect seen in the data. I pointed out

that by using such a scheme we will run into the problem of testing some

subjects too soon and some too long after the previous test, and this may

lead to carryover and/or avoiding detection of certain drug abuse episodes.

In addition, differences in missed visit rates and/or treatment effect across

the different days the urine specimens are collected provide some useful

information, and such differences should be expected. Even if the treatment

is working, subjects can be expected to abuse more during weekends than

during weekdays because of social pressures, etc.; the effectiveness of

treatment may be expected to diminish during weekends.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

45
Efficacy of Urinalysis in Monitoring

Heroin and Cocaine Abuse Patterns:

Implications in Clinical Trials for

Treatment of Drug Dependence

Edward J. Cone and Sandra L. Dickerson

INTRODUCTION

Human self-administration of drugs of abuse begins a series of biochemical

and pharmacologic events that culminates in the alteration of an individual’s

mood state. The physical and chemical processes that ultimately determine

the extent of drug effect, that is, how much active drug accumulates in the

drug-receptor biophase, also serve to terminate the drug’s actions. The primary

processes responsible for the appearance and termination of these effects are

absorption, distribution, metabolism, and excretion. The time courses of these

processes are illustrated in the generic example shown in figure 1, panel A,

for the appearance and disappearance of a drug in urine. Urine drug levels

typically increase rapidly after administration and peak and decline at a

slower rate. In this example, the analytical technique used to measure drug

levels has an assigned cutoff of 300 ng/mL. Cutoffs are used to categorize

urine specimens as positive or negative for drug; they are assigned based on

analytical factors such as assay precision and reproducibility and on therapeutic

considerations such as drug potency and rate of excretion. For opiates and

cocaine, 300 ng/mL was selected as the screening cutoff for use in Urine testing

of Federal employees (Mandatory guidelines 1988). This cutoff is in common

use throughout Federal and private-sector employee testing programs and in

treatment programs.

As shown in figure 1, urine drug levels had declined to the cutoff by 36 hours

after drug administration. All urine specimens obtained prior to that time would

have tested positive. This is an ideal example of a detection time for a drug

obtained by urine testing; this time interval represents the time elapsed from

drug administration to excretion of the last positive specimen. This concept is

extremely useful when implementing a drug testing program for treatment of

drug addicts or conducting a clinical trial for a new medication. In these

46
FIGURE 1. Illustration of drug absorption, distribution, metabolism, and

excretion phases for a short-acting drug during excretion in urine

(panel A) and relationship of detection time to cutoff selection

(panel 6)

situations, it is vitally important to know whether illicit drugs are being used.

Urine testing is recognized as the most objective means of diagnosing recent

drug use (Hat-ford and Kleber 1978). Detection of a short-acting psychoactive

substance such as heroin or cocaine in urine obviously indicates recent usage.

In clinical trials that test drug-abusing subjects, the absence of drug use

47
generally indicates a successful outcome, whereas multiple drug use patterns

indicate failure. In many situations, the degree of success may be judged on

the basis of the number of positive urine test results obtained during the course

of the clinical trial.

This chapter reviews the usefulness of detection times in relation to the

conduct of clinical trials of new medications designed for the treatment of

drug dependence. A fixed-interval urinalysis schedule is proposed, which

optimizes the chances of detection of cocaine and/or heroin use while

minimizing the risk of overlap of test results from a single episode of drug

self-administration. Although random-interval schedules have been proposed

as being more efficient for detection of illicit drug use in treatment (Goldstein

and Brown 1970; Harford and Kleber 1978), it appears unlikely that the randominterval schedule would provide sufficient coverage for estimation of the extent

of drug use. Hence, only fixed-interval schedules are considered in this

chapter.

INFLUENCE OF DOSE AND CUTOFF ON DETECTION TIMES

There are many pharmacologic and chemical factors that influence detection

times (Gorodetzky 1977). Pharmacologic factors include drug dose, route

of administration, pH of the biological fluid, and individual differences in rates

of metabolism and excretion. Chemical factors that relate to the analytical

technique used for drug detection include selection of the cutoff, assay

precision, specificity, and accuracy. The authors have systematically studied

the influence of two of these factors, cutoff and dose, on detection times of

cocaine and opiates. Figure 2 illustrates the influence of cutoff on the detection

time of cocaine following administration of a 20-mg intravenous (IV) dose of

cocaine hydrochloride. As the cutoff is lowered (greater assay sensitivity), the

detection time increases (drug is detected longer). Figure 3 is a combined plot

illustrating the changes in detection times of cocaine (panel A), morphine (panel

B), heroin (panel C), and codeine (panel D) on a linear scale. The incremental

changes in detection time with cutoff appear to be linear for cocaine and

codeine and curvilinear for morphine and heroin. Regardless of the shape of

the curve, these increases in detection time with the lowering of the cutoff are

substantial. Clearly, the selection of the cutoff will have a major impact on the

period of drug detectability. Consequently, outcome comparisons of clinical trial

results between participating centers can be made only when identical cutoffs

are utilized. In most cases, the recommended cutoffs by the U.S. Department

of Health and Human Services Mandatory Guidelines (Mandatory guidelines

1988) should be used since most commercial assays are targeted toward and

perform best at these concentrations. Also, since substantial differences occur

in immunoassay specificity from different commercial vendors (Cone and

48
FIGURE 2. Mean detection times at different cutoffs for cocaine (20-mg IV

dose) by EMIT d.a.u. cocaine analysis. Error bars represent

standard error of the mean (n=4).

Mitchell 1989; Cone et al. 1992), identical urinalysis technology should be

employed by each participating center.

For pharmacokinetic reasons, there is a log-linear relationship between drug

dose and detection times. Consequently, detection times increase by one halflife each time the drug dose is doubled. For example, if the detection time of a

3-mg dose of heroin is 14.5 hours (300ng/mL cutoff) and the urinary excretion

half-life of morphine (the analyte tested for heroin use) is approximately 6 hours,

the detection time should increase to 20.5 hours when a person administers a

6-mg dose. The data illustrated in the bar graph in figure 4 indicate that the

mean detection time of heroin for six subjects actually increased to 21.8 hours.

For morphine, the mean detection time (n=6) increased from 34 hours for a

10-mg dose to 44 hours for a 20-mg dose. For codeine, the mean detection

time (n=4) increased from 48 hours for a 60-mg dose to 54 hours for a 120-mg

dose. These data are convincing evidence that a log-linear relationship exists

49
FIGURE 3. Relationship of cutoff to detection times for cocaine, morphine,

heroin, and codeine

between dose and detection time for these drugs. Because of this relationship,

changes in drug dose by the user alters detectability of drugs by urinalysis only

slightly. This is fortuitous since the magnitude, frequency, and nature of illicit

drug use by participating subjects are major variables in controlled clinical trials.

FREQUENCY OF TESTING VS. “SAFE TIME”

The dilemma in deciding how many times per week to test subjects arises

from the need to maximize the chances of drug detection while minimizing

the chances of counting a single drug use incident as two episodes and also

minimizing the financial costs to the program and the inconvenience to subjects

and staff. Figure 5 illustrates the amount of time during a week that a subject

can use cocaine without being detected if testing is performed once per week.

In this example, the mean detection time of 35.8 hours for cocaine (Cone et al.

50
Codeine

(n=4)

Morphine

(n=6)

Heroin

(n=6)

Detection Time (hours)

FIGURE 4. Mean detection times by EMIT d.a.u. analysis vs. dose (300-ng/

mL cutoff) of codeine, morphine, and heroin

1989) is used; hence, if the subject uses cocaine in this time period prior to

testing on Friday, drug use will be detected. Drug use during any other part of

the week will not be detected, resulting in a total of 132.2 hours of “safe time.”

Obviously, the amount of safe time varies with the drug testing schedule.

Figure 6 illustrates the amount of safe time arising from different weekly

schedules of cocaine testing. If testing were performed 7 days a week,

nearly all drug use would be detected; however, this is impractical in most

cases because of subject, staff, and financial limitations. Furthermore,

detection times for cocaine and heroin can extend beyond 24 hours; hence,

drug excretion following a single use would extend through the next testing

session, and a single use would be mistakenly counted twice. In contrast, an

infrequent testing schedule would miss a substantial amount of illicit use and

the urine data would be fallacious.

Figure 7 illustrates the amount of safe time (%week undetected) for cocaine

and opiates for testing schedules varying from zero to 7 test days a week.

It is apparent for three of the four drugs that there is an inflection in the graph

at the 3-days-per-week schedule. Only heroin showed a linear decline. This

51
FIGURE 5. Illustration of safe time and detected time for a once-a-week

testing schedule for cocaine. It should be noted that, a/though

testing was performed on Friday in this example, the results

would have been identical for any other test day of the week.

is likely due to the small doses employed in the heroin study resulting in

minimal detection times. For morphine, codeine, and cocaine, the amount of

safe time declined rapidly from zero to the 3-days-per-week testing schedule.

Thereafter, the amount of safe time decreased more slowly. Consequently, it

appears that a 3-days-per-week schedule provides the most parsimonious

approach to testing when considering how to minimize both safe time and

excretion overlap at the same time.

RANDOM DRUG USAGE VS. DIFFERENT URINE TESTING SCHEDULES

If a drug-abusing subject self-administers a single dose of cocaine during the

course of a week, will the selected drug testing schedule detect drug abuse?

This question was tested by generating four sets of 100 randomly selected

times during a given week in which a subject might administer cocaine. No

restrictions were placed on the time of drug use. A mean detection time of

35.8 hours was used in the calculation of %drug episodes detected. Individual

and mean data are shown in table 1 for different testing schedules. The mean

%drug episodes detected increased in a linear fashion from zero (no test days)

to 63 percent with a 3-days-per-week schedule (Monday, Wednesday, Friday).

Thereafter, the increase slowed and culminated in 100 percent of drug episodes

detected with a 7-days-per-week schedule. Carryover from test to test as a

result of the single drug dose did not begin to occur until the number of test

days increased to 4 days per week. Thereafter, carryover increased

substantially to nearly 50 percent with a 7-days-per-week schedule.

52
FIGURE 6. The relationship of %safe time to the urinalysis testing schedule.

Test days are indicated by an asterisk.

A second analysis of urine testing schedules was performed by simulating

two random cocaine uses occurring during the same week. The time between

the two doses was varied from 6 hours to 84 hours. Sets of 100 randomly

selected times, separated by the minimum interval between cocaine use, were

generated. The effectiveness of testing three times per week was compared

with testing only once per week. The numbers of times that two uses resulted

53
FIGURE 7. Relationship of drug testing schedules to %week undetected for

cocaine, morphine, heroin, and codeine (EMIT d.a.u. analysis,

300-ng/mL cutoff)

in 0, 1, and 2 positive results are shown in table 2 along with the number of

times that two uses occurred within the same detection time period resulting in

a single positive result. When the testing schedule called for only 1-day-perweek testing, a substantial amount of drug use went undetected. The number

of times that no drug use was detected varied from 64 to 39 percent depending

on the time interval between uses. Positive results ranged from 36 to 61

percent. There were only a few occurrences of random multiple drug use

occurring within the same detection time.

With a 3-days-per-week testing schedule (Monday, Wednesday, Friday),

detection efficiency increased substantially over the 1 -day-per-week testing

schedule. The number of times that no positive results were obtained by the

3-days-per-week schedule varied from 6 to 16 percent. Single positive results

54
TABLE 1.

Urinalysis

Testing

Schedule

M 11 3 18 26 22 20 0

M,Th 2 34 32 47 48 41 0

M,W,F 3 61 53 67 66 63 0

M,W,Th,F 4 68 59 75 74 69 13.8

M,T,W,Th,F 5 77 69 81 81 79 26.3

M,T,W,Th,F,Sa 6 93 89 95 95 93 33.0

M,T,W,Th,F,Sa,S 7 100 100 100 100 100 48.3

Effect of urinalysis testing schedules on detection of a single

cocaine use during a week of testing*

%Drug Episodes Detected

Tests/ Trial Trial Trial Trial

Week #1 #2 #3 #4

Average Single

Drug Use

Episodes (Percent)

Resulting in Two

Mean Positive Tests

*Each trial consists of 100 randomly generated times during the week that a

person might self-administer a single dose of cocaine. A detection time of

35.8 hours was used in the determination of %drug episodes detected.

(one use went undetected) were obtained between 43 to 60 percent of the

time, and double positive results (both uses were detected) were obtained at a

frequency of 27 to 45 percent. When the single and double positive results are

combined, the efficiency of detection of cocaine use for the week averaged

87.3 percent across the different drug use patterns. There were a maximum

of seven instances of drug use occurring in the same detection time window

when the second drug use could occur within 6 hours of the first use. In these

instances, two uses appeared as a single use from the testing result. As the

drug use interval lengthened to 24 hours, this phenomenon disappeared and

was no longer a problem.

The data shown in tables 1 and 2 were generated to challenge the earlier

conclusion that a 3-days-per-week schedule was the best compromise

between maximizing drug detection and minimizing carryover. A Monday,

Wednesday, Friday testing schedule demonstrated a mean efficiency of 63

percent in detecting single incidents of cocaine use. The increase in efficiency

by further testing was relatively minimal until the frequency was increased to 6

days or more per week. Carryover of drug use from one test to another was not

a factor with the Monday, Wednesday, Friday testing schedule but did occur at

higher frequency testing schedules. When multiple cocaine use was simulated,

that is, 2-times-per-week separated by a minimum time interval, the 6-daysper-week testing schedule was substantially better than a 1-day-per-week

schedule.

55
TABLE 2. Effect of urinalysis testing schedules on detection of two cocaine

uses separated by a minimum hourly interval between uses during

a week of testing*

*Each trial consisted of 100 randomly generated time pairs (separated by a

minimum interval) during the week that a person might self-administer two single

doses of cocaine. A detection time of 35.8 hours was used in the determination of

number of positive results.

SUMMARY AND CONCLUSIONS

Urinalysis can be used as an objective criterion for monitoring the outcome

of a treatment program or a clinical trial. Important factors to consider when

implementing a drug testing program include standardization of assay

technology and cutoffs between participating centers and selection of identical

testing schedules. Also, it is vitally important to minimize the amount of safe

time (time that drug use can go undetected) occurring in a testing schedule.

The detection times for cocaine and heroin have been shown to vary with

selection of cutoff and with the drug dose. Obviously, the selection of cutoffs is

under program control, whereas the amount of illicit drug use is under subject

control. Fortunately, changes in the illicit drug dose by the subject demonstrate

a log-linear relationship to detection time. Hence, a higher drug dose by the

56
subject only extends the detection time slightly (and improves the probability of

detection) without greatly increasing the risks of drug carryover from one urine

test to another.

The most efficient testing schedule for judging the outcome of clinical trials

for cocaine and heroin appears to be a 3-days-a-week schedule (Monday,

Wednesday, Friday or Tuesday, Thursday, Saturday). When different

schedules were challenged by simulating random times at which cocaine

use might occur during the week, the 3-days-per-week schedule was the

most efficient without the risk of carryover. The 3-days-per-week schedule

also performed better than 1-day-per-week when multiple random drug use

was simulated. Overall, the 3-days-per-week testing schedule with specified

assay technology and cutoffs was the best compromise for maximizing

detection of drug use, minimizing carryover, and providing a standardized

methodology for outcome comparison between programs.

REFERENCES

Cone, E.J.; Dickerson, S.; Paul, B.D.; and Mitchell, J.M. Forensic drug testing

for opiates: IV. Analytical sensitivity, specificity and accuracy of commercial

urine opiate immunoassays. J Anal Toxicol 16:72-78, 1992.

Cone, E.J.; Menchen, S.L.; Paul, B.D.; Mell, L.D.; and Mitchell, J. Validity

testing of commercial urine cocaine metabolite assays: I. Assay detection

times, individual excretion patterns, and kinetics after cocaine administration

to humans. J Forensic Sci 34:15-31, 1989.

Cone, E.J., and Mitchell, J. Validity testing of commercial urine cocaine

metabolite assays: II. Sensitivity, specificity, accuracy and confirmation by

gas chromatography/mass spectrometry. J Forensic Sci 34:32-45, 1989.

Goldstein, A., and Brown, B.W., Jr. Urine testing schedules in methadone

maintenance treatment of heroin addiction. JAMA 214:314-315, 1970.

Gorodetzky, C.W. Detection of drugs of abuse in biological fluids. In: Born,

G.V.R.; Eichler, O.; Farah, A.; Herken, H.; and Welch, A.D., eds. Handbook

of Experimental Pharmacology. Vol. 45. Berlin: Springer-Verlag, 1977. pp.

319-409.

Harford, R.J., and Kleber, H.D. Comparative validity of random-interval and

fixed-interval urinalysis schedules. Arch Gen Psychiatry 35:356-359, 1978.

Mandatory guidelines for Federal workplace drug testing programs; final

guidelines; notice. Federal Register 53:11970-11989, Apr. 11, 1988.

ACKNOWLEDGMENT

Dr. Nancy L. Geller of the National Heart, Lung, and Blood Institute reviewed

and commented on the manuscript.

57
AUTHORS

Edward J. Cone, Ph.D.

Chief

Laboratory of Chemistry and Drug Metabolism

Sandra L. Dickerson, B.S.

Medical Technologist

Addiction Research Center

National Institute on Drug Abuse

P.O. Box 5180

Baltimore, MD 21224

58
Comments on “Efficacy of Urinalysis

in Monitoring Heroin and Cocaine

Abuse Patterns: Implications in

Clinical Trials for Treatment of Drug

Dependence” by Cone and Dickerson

Nancy L. Geller

Cone and Dickerson consider fixed-interval scheduling for drug use monitoring

in trials for treatment of drug dependence. They conclude that changes in drug

dose by the user alter detectability of drugs by urinalysis only slightly and that

the Monday, Wednesday, Friday monitoring schedule is optimal because it

maximizes the chance of detection of an episode of drug use and minimizes

the chance of having two detections of the same episode.

The conclusion that dose alters detectability only slightly assumes a log-linear

relationship between drug dose and detection times. This is equivalent to

a one-compartment pharmacokinetic model. The data for morphine and

heroin in Cone and Dickerson’s figure 3 (this volume) suggest that a higher

order compartmental model might be more appropriate. Such a possibility

should be investigated.

The authors’ conclusion that the Monday, Wednesday, Friday test schedule is

optimal rests on certain assumptions:

1. If there is any episode of drug use, the test schedule should be able to

detect it most of the time.

2. Detection of drug use within approximately 36 hours of that use is certain;

that is, there are no false negatives.

3. Having two tests detect one episode of drug use should be avoided if

possible.

59
TABLE 1.

Urinalysis

Testing

Schedule

None

M

M,Th

M,W,F

M,W,TH,F

Effect of urinalysis testing schedules on detection of a single random episode of cocaine use during a

week of testing*

Simulated Probability of

Simulated Probability of Drug Episode Resulting Actual Probability of

Detection of Drug Episode Actual Probability of in Two Positive Tests Drug Episode Resulting

(n=400) Detection of Drug Episode (n=400) in Two Positive Tests

0 0 0 0

.20 .213 0 0

.41 .426 0 0

.63 .639 0 0

.69 .712 .138 .140

M,T,W,Th,F .79 .785 .263 .281

M,T,W,Th,F,Sa .93 .927 .330 .351

Every day 1.00 1.00 .483 .492

*A detection time of 35.8 hours and a zero probability of false negative tests were assumed in both the simulations and calculations.
4. If drug use is detected, there has indeed been drug use; that is, there are

no false positives.

5. Drug detection will be done in multiples of 24 hours,

The probabilities that are simulated, according to the assumptions above,

can be calculated exactly and are shown in table 1. As in the simulations,

the exact calculations assumed that an episode of drug use is equally likely

to occur at any time during the week (i.e., uniformly distributed). However, a

trial participant who is going to take the drug may recognize that he or she is

less likely to test positive next time if the drug is used soon after a urine test.

Similarly, the probabilities of the model assumed for Cone and Dickerson’s

table 2 (this volume) can be explicitly calculated, but again, the times of an

episode of drug taking may not be uniformly distributed.

Simulation is a rich tool and could allow more complicated scenarios to be

evaluated, including nonuniform times of drug use. The possibility of false

positives and false negatives could be built into a simulation model, which is

equivalent to varying the cutoff for detection from 300 ng/mL. Testing at more

than one time of day, such as mornings or afternoons, could also be evaluated.

Software for simulating stochastic processes, such as the General Purpose

Simulation System, might be used so that, in addition, random test times could

be assessed.

The conclusions in Cone and Dickerson’s chapter follow logically from their

assumptions. However, more complex assumptions might be more realistic

and could be considered in further work.

ACKNOWLEDGMENT

Dean A. Follmann, Ph.D., National Heart, Lung, and Blood Institute, National

Institutes of Health, is acknowledged for helpful discussions and for presenting

these comments at the technical review in my absence.

AUTHOR

Nancy L. Geller, Ph.D.

Chief

Biostatistics Research Branch

National Heart, Lung, and Blood Institute

National Institutes of Health

Federal Building, Room 2A-11

7550 Wisconsin Avenue

Bethesda, MD 20892

61
Summary of Discussion: “Efficacy of

Urinalysis in Monitoring Heroin and

Cocaine Abuse Patterns: Implications

in Clinical Trials for Treatment of Drug

Dependence” by Cone and Dickerson

Ram B. Jain

Dr. Weng suggested that blood samples from each subject be obtained

prior to entry into the trial so that their individual pharmacokinetic profiles

could be studied and their metabolic rates evaluated. The differences in

metabolic rates will have a bearing on the detectability of drugs in urine.

Individual pharmacokinetic profiles could also be used to appropriately

schedule collection of urine samples. This suggestion was appreciated;

however, as pointed out by Dr. Johnson, it is not practical to obtain blood

samples from every subject, since some have poor venous access due to

abuse of their veins from frequent injections. In addition, the process of

randomization should equally distribute fast and slow metabolizers across

different treatment groups,

Dr. Wright inquired about the cross-reactivity between opiates of abuse and

replacement (treatment) opiates (and over-the-counter drugs) in immunoassays

and about the need for confirmatory testing. According to Dr. Cone, the

probability of false positives in immunoassays to detect opiates is very small

unless a subject is using codeine. Use of a confirmatory assay such as gas

chromatography/mass spectrometry would add little unless there was a need

for quantitative data.

Dr. Gorodetzky asked if, in testing an individual by immunoassay following

drug usage, negative results could be followed by positive results. It was

acknowledged that this does not happen very often except with marijuana.

Dr. Fisher suggested that urine specimens be collected every day to collect the

maximum amount of information. He suggested that this information could then

be used to more appropriately interpret and/or modify information obtained from

62
Monday, Wednesday, and Friday specimens. He also suggested the need

for estimating the amount of opiates used by using a method such as

area under the curve. This method is probably impractical since many

urine specimens would have to be collected over time, or timed plasma

specimens with knowledge of duration since injection and amount of drug

injected would be required. Dr. Johnson said different subjects may need

different amounts of opiates to have the same effect, and because of risk of

human immunodeficiency virus infection from intravenous injection of drugs

using shared needles, it is important to know the exposure frequency and what

the treatment drug can do to reduce this frequency.

Dr. Gordon also proposed to collect urine specimens more often than three

times a week and, based on the results of a certain number of successive

specimens (e.g., positive, negative, positive, positive), develop an algorithm

to decide whether two or more consecutive positive specimens represent

independent episodes of drug abuse or carryover. The proposal was well

taken, but the same algorithm cannot be applied to all subjects since the

probability of carryover varies from subject to subject. Such an algorithm

has the potential to underestimate the probability of drug abuse. However,

such an algorithm used in conjunction with self-reported drug use might be a

possibility.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville. MD 20857

63
Open/Panel Discussion: Design

Issues

Ram B. Jain

Panel Members: A.S. Hedayat (Chair), Albert J. Getson, Alan J. Gross,

Sudhlr Gupta, Don Jasinski, Mel-Ling Ting Lee, Carol K. Redmond, and

Margaret Wu

The three primary issues discussed were:

Fixed time vs. random time sampling, including sampling frequency

Estimation of carryover

Estimation of the amount of drug abuse

FIXED TIME VS. RANDOM TIME SAMPLING

It was opined that the objectives of the clinical trials would determine the

adequacy of fixed or random time sampling. If the objective was merely to

evaluate the efficacy of a treatment drug, fixed time sampling would probably

be the sampling scheme of choice. If determination of the effectiveness of the

treatment drug was the objective of the trial, then random time sampling would

probably be the sampling scheme of choice.

It was pointed out that determination of pharmacological efficacy of a

treatment drug was the primary objective of a clinical trial such as the ARC

090 trial completed at the Addiction Research Center. The pharmacological

efficacy was primarily evaluated by posttreatment frequency of drug abuse.

However, as pointed out by Dr. Johnson, variables such as retention rates,

withdrawal symptoms and signs, and opiate- and cocaine-craving scores

were also evaluated in the ARC 090 trial.

Since the frequency of drug abuse is not directly measurable, frequency of

detected drug (ab)use from urine samples on a per-sample or per-week basis

is the surrogate measure used to represent posttreatment frequency of drug

abuse. Using this surrogate measure, it is possible that multiple episodes of

drug abuse are counted as one, but this is the limitation of the sampling

64
techniques currently used. In addition to reduction in the frequency of drug

abuse, as Dr. Vocci mentioned, there is also interest in knowing when the

treatment drug starts working. Some individuals in the buprenorphine and

methadone 60 mg arms of the ARC 090 study stopped abusing drugs almost

immediately and remained drug-free throughout the trial. Some individuals

need to build a reservoir of treatment drug in the body before the drug shows

its effect; it takes these individuals some time (4 to 6 weeks) before they stop

abusing drugs. Eventually, a receptor occupancy may be reached for all

individuals that may be consistent with no more drug (ab)use.

Since agonists, partial agonists, and antagonists act differently, there is also

interest in evaluating the pattern of cessation of drug abuse, that is, the pattern

of positive and negative urine samples. There is interest in being able to know

if some daily users are being converted to weekend users only, for example, the

maximum duration for which they can remain drug-free. For example, one of

the outcome variables analyzed for the ARC 090 trial was the time to the (first)

drug-free period of 28 days or more as determined by negative urines.

However, as pointed out by Drs. Wright and Getson, it is critical to remember

that reduction in frequency and/or amount of drug abuse is only a small part

of the claims that can be made for a treatment drug. These medications may

also alter symptoms of drug (ab)use; suffering from drug (ab)use; social

functioning (behavior) such as employment stability, family life, and crimerelated activities; or target behaviors such as needle sharing and injection

of illicit drugs. Evaluation of efficacy should be married to the development

of the treatment compound as a whole. Efficacy trials should be followed by

effectiveness trials, which may focus more on the sociological behaviors, as

mentioned earlier. For these effectiveness trials, random time sampling may

be the sampling scheme of choice. These effectiveness trials should lead

to a broader understanding of the compound as a whole. An efficacy trial

determines whether or not the drug works; an effectiveness trial generates

additional information helpful in writing a good label (package insert) for the

treatment drug.

An efficacious drug in the hands of a good clinician would work more effectively

since these clinicians are likely to supplement treatment drugs with services

such as family and/or employment counseling. However, if these effectiveness

variables are allowed to interact with efficacy variables in the efficacy trials, the

sample size requirements would become prohibitive and it may not be possible

to show the pharmacological efficacy of the treatment drugs. It was suggested

that efficacy trials may include an additional treatment arm in which subjects get

other services, such as counseling, after only 2, 4, or 8 weeks of drug therapy.

65
If frequency of detectable drug abuse is the primary outcome variable in an

efficacy trial, the drug abuse phenomenon should be viewed on a continuum,

and as such, fixed time sampling should be appropriate. In fact, Dr. Fisher

strongly favored collection of urine samples more often than three times a

week, probably every day, since more information is generally better. However,

collecting urine samples too often may have a negative effect on dropout

rates and will shape the patient population remaining in the trial in such a

way that generalizations to the addict population-at-large may be difficult. In

fact, dropout rates are substantial (as much as 60 to 80 percent) in these trials.

Cost may be another factor that should be considered. A compromise may be

to do less frequent sampling in those who remain in the trial for a certain period

and get as much information as possible on those who dropped out by sending

out nurses, social workers, etc. There was a strong feeling that additional

information should be obtained on those who drop out of the trial because,

with dropout rates as high as they are in these trials, there certainly is a serious

problem in making inferences for the total addict population. Also, such high

dropout rates make it difficult to do an intent-to-treat analysis.

Dr. Jasinski pointed out that clinical trials are unique experiments as opposed

to drug treatment programs. The lack of resources (financial and others) and

practical considerations such as frequent collection of urine samples, if desired,

should not stand in the way of doing these experiments. Resources should be

obtained and study centers identified where these experiments can be

successfully conducted.

There were other arguments in favor of and against both fixed and random

time sampling. It was suggested that fixed time sampling results in nonrandom

missed observations. Since missing at random may be an assumption required

to do some analyses, this may create a potential bias in these analyses.

However, even in random time sampling, addicts are able to determine how

often they will be tested and when, and thus, even random time sampling

cannot ensure random missed observations. The data do not exist to show

which type of sampling leads to higher noncompliance, including dropout rates.

It may be that it is just the frequency (e.g., once a week vs. five times a week)

of urine collection, irrespective of the type of sampling, that has a bearing on

the noncompliance problem. In fixed time sampling, staffing requirements (to

collect urine samples) are known in advance, which helps in planning for

resources. A Food and Drug Administration audit of a trial done using fixed

time sampling is relatively easier to conduct. Also, the choice between fixed

time and random time sampling may be a choice between dealing with a

possible treatment by day interaction and a relatively large error term (noise).

Fixed time sampling may be used to collect data from some experimental units,

and random sampling may be used to collect data from other experimental

66
units. But analysis of these data may present unknown challenges and

possible interpretation problems. Alternatively, the data may be collected

frequently using fixed time sampling, and only randomly selected data points

may be used for analyses, In addition, irrespective of the type of sampling

used, a clinical trial that has the ability to test (internally validate) some of the

assumptions used in the analyses is preferred over one that does not have

such an ability.

It was brought to attention that, since efficacy trials do not have any negative

contingencies associated with results of urine samples, the question of whether

data are missing at random may be a nonquestion since addicts may not have

a reason to miss clinic visits. Dr. Blaine agreed. He explained that in their

gepirone study, which did not have any negative contingencies associated

with urine results, patients’ admission of drug (ab)use matched urine test results

most of the time. However, he added that absence of negative contingencies

amounts to permission for drug abuse, as can be seen from the substantially

higher percentage of positive urines (60 to 70 percent) from one of their

buprenorphine trials, which did not have negative contingencies, compared

with some treatment clinics (10 to 12 percent positive urines), which do have

negative contingencies. Dr. Vocci emphasized that “if you are looking for

efficacy in a clinical trial, you are better off . . . allowing individuals to use

[drugs] in a manner that is not proscribed by the policies of the clinic.”

Artificially controlling drug abuse may result in prohibitive sample size

requirements if a pharmacological effect is to be shown.

It was also suggested that the question of fixed vs. random time sampling

should be decided by simulation methods using known pharmacokinetic

profiles of the drugs that the urine samples are supposed to detect. These

simulation methods may allow for a permissible degree of carryover and an

inability to detect episodes of drug abuse. However, since pharmacokinetic

profiles of the drugs of abuse are dose dependent and the dose and timing of

drugs consumed by an addict are not known, such an exercise may be very

difficult.

ESTIMATION OF CARRYOVER

It was mentioned that, in addition to a parallel design, a crossover design

should be considered. A crossover design may be able to better handle the

problem of carryover. However, as Dr. Hedayat pointed out, crossover designs

have their own problems in interpretation of results. Parallel designs may be

used to answer certain questions, whereas crossover trials may be designed to

answer other questions.

67
Dr. Mei-Ling Lee visualized the problem in a different way. She observed

that in these trials researchers are working with a mixture of distributions, and

data should be analyzed as a mixing distributions problem. However, to

analyze these data as a mixture of distributions, an estimate of the amount

of drug present in the urine or plasma samples will be needed. Dr. Follmann

agreed. Binary data would not be sufficient. Dr. Collins commented that,

unless the timing of the episodes of drug abuse is known, concentration

profiles of drug in the urine or plasma samples may not be fully informative.

And as such, information obtained from pharmacokinetic profiles may have to

be supplemented with that obtained by asking the addicts about the timing of

drug abuse, if any, each time he or she is asked to provide a urine or plasma

sample.

If binary data must be used, information obtained from a self-reported

measure of drug abuse (e.g., “Did you use the drug during the last 24

hours?“) when combined with the urine results may be able to help decide

if a carryover existed. Dr. Wright suggested we should be looking for other

sources of information, such as the staff and clinicians present at the time of

clinic visits, The clinic staff should be able to judge if the subject may or may

not have abused the drugs since the last clinic visit or since the last time a

urine specimen was provided. Various pieces of information from various

sources, including urine test results, can be put together according to a certain

predefined set of rules and converted into some sort of scores that may be

interpreted as a new episode of drug abuse or a carryover from the previous

episode.

ESTIMATION OF THE AMOUNT OF DRUG ABUSE

A reduction in the frequency of drug abuse does not guarantee reduction in the

amount of drug abuse. A daily user may be converted to an occasional user,

but he or she may still be using the same amount of drug. Instead of using the

same amount in, for example, 10 episodes, he or she might be using the same

amount in 5 episodes. However, the binary data currently obtainable from urine

assays cannot provide estimates of the amount of drug abuse. Hence, it was of

interest to discuss this issue of being able to estimate the amount of drug

abuse.

There was a strong sentiment at the meeting against attempts to estimate drug

consumed from the drug present in the urine samples. As Dr. Gorodetzky put it,

“Do not ask too much from a qualitative urine. You can be as precise as

you want in terms of quantity of morphine in a . . . urine sample. It is not going

to tell you a. thing about how much drug was taken, when and how many

times. You cannot do it . . . There are some theoretical models you can build,

68
if you knew what time, when the time of drug administration was, if you knew

when patients urinated, what the time was since last urination, what the volume

was in this timed collection. Then maybe, if you had good enough data on

which to base it, you could make some inferences. Right now, it cannot be

done.” Dr. Jasinski expressed similar sentiments.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

69
A Bayesian Nonparametric Approach

to Analysis of Treatment for

Drug-Dependence Data

Ram C. Tiwari

INTRODUCTION

In the National Institute on Drug Abuse ARC 090 trial to evaluate the efficacy of

buprenorphine as compared with methadone 20 mg, and methadone 60 mg for

treatment of opiate dependence, urine samples were obtained from patients

three times (Monday, Wednesday, and Friday) every week for a period of 25

weeks. During the first 17 weeks of the study, the patients were maintained on

the treatment drug; during the rest of the study, they were detoxified from the

treatment drug. The urine samples were assayed for the presence of opiates.

This chapter analyzes the data set collected from the first 17 weeks. As each

dose of a treatment drug provides one observation, a maximum of 51 urine

samples were obtained from each patient. The data also contain some missing

observations due to no-shows during the course of study or due to withdrawals

from the study. The accommodation of missing observations is an important

issue and so is the use of information from the withdrawals from the study. To

accommodate some missing observations, we have reduced 5 1 -dimensional

data to 17-dimensional data by developing a weekly index of urine samples

being positive or negative (see, also, Jain, this volume). A week is considered

to be negative for opiates if at least two observations in this week are negative.

Otherwise, the week is considered to be positive for opiates. Thus, the weeks

with censored observations and two or more missing observations are

automatically considered to be positive. This assumption does result in some

loss of information, e.g., one who has three negative urines during a week is

treated the same way as one who has only two negative urines during the week.

The next section presents a Bayesian approach to analysis of the binary

response data. The analysis of ARC 090 trial data is presented in the last

section.

70
BAYES ESTIMATION

Here, we consider a Bayesian nonparametric approach to the estimation of the

conditional probabilities of the binary responses. To simplify the notations,

denote a typical point (t1

, . . .,tr) of the product space by

(r = 1,2,. . .). By denote the point in that is obtained by augmenting

by 0, that is, and similarly for Finally, denote by the

cylinder set of all points in whose first r coordinates form the

vector that is,

Let be the collection of the empty set and the finite disjoint unions of cylinder

sets form an increasing sequence of -fields,

and is a field. The -field is the smallest -field

containing

Consider a sequence of blocks of numbers in the closed unit interval [0,1]:

For and Define a

probability measure on such that

(Here and throughout is interpreted as the empty sequence, i s

interpreted as .) Then, it can be checked that

Thus, the restriction of uniquely extends to a

probability measure

Let be the space of all blocks with its coordinates lying in [0,1]. If

is equipped with the product then the map defines a

transition function from into Consider a probability measure

such that, under the coordinates of are mutually

independent with

71
where Beta( b) denotes a Beta distribution with parameters and b, then,

under , the random probability measure is said to have a Polya tree

process (Ferguson 1974). The posterior distribution of a Polya tree process,

given an observation, is also a Polya tree process and is obtained by updating

one of the Beta distributions at each level of the tree.

If in (3) is a finite measure on then, under the joint distribution of

is a Dirichlet distribution with parameter

(see Basu and Tiwari 1982). Furthermore, if

is a partition of then

have a Dirichlet distribution with parameters

implies that

The following result is useful.

Theorem 1. (Blackwell 1973). The random probability measure is a

Dirichlet process on with parameter

To prove theorem 1 it suffices to show that, for arbitrary measurable partition

the distribution of

Dirichlet distribution with parameters

Ferguson 1973). This follows from the following lemmas.

Lemma 1. Let be an arbitrary set in Then, under the assumption (3), the

random variable has a Beta distribution.

Proof. Let distribution}. Then,

by definition It is easy see that contains Also, is a monotone

class. To see this, let be an increasing sequence of sets in and let

Then, clearly and by continuity from below

for each as which is a stronger result than the

convergence in distribution. Again, since all finite moments of the random

variable converge to the corresponding moments of a random variable

X, say, having distribution. Hence, For a decreasing

sequence of sets in we argue in a similar way. Thus, is a monotone class

containing the field and hence contains the smallest -field containing

Lemma 2. For any arbitrary finite partition

measurable sets, the random variables have

the Dirichlet distribution with parameters

Proof. By an approximation theorem (see, Billingsley 1979, Theorem 11.4,

72
p. 140) there exists a sequence of partitions of

into measurable sets such that

Also, from Lemma 1, the random variable has a

distribution, j = 1, 2, . . . , k. Therefore, for

j = 1, 2 , . . . , k, we have

since Thus, the random

variables converge in probability and hence

in distribution to the random variables Since,

for each n, the random variables have a Dirichlet

distribution with parameters and all finite

moments of converge to the corresponding

moments of the random variables say, having a Dirichlet

distribution with parameters it follows that

have a Dirichlet distribution with parameters

For more on the Dirichlet process, see Ferguson (1973, 1974) or a recent

survey article by Ferguson and colleagues (1992).

into [0, 1] induces a random

probability measure on [0, 1]. If is a Polya tree process on then the

induced random probability measure on [0, 1] is also a Polya tree process.

Furthermore, if

(4)

then the induced random distribution function on [0, 1] is absolutely continuous

w.p. (cf. Kraft 1964 and Métiviar 1971). If is a Dirichlet process on

with parameter , then (4) simplifies to

(5)

Suppose there are m patients involved in the study on a treatment.

Corresponding to the ith patient, let denote the vector of

observations on the response variable taking on only two values: 1 =

presence, and 0 = absence of opiate. Thus, Let

73
Given

function of is

observations from Then, the likelihood

where and

is the degenerate measure at

Clearly, under

Furthermore, from (3) and (6) it can be easily checked that the coordinates of w

are mutually independent a posteriori, and

and

From (2), (3) and (7) it follows that if is a Polya tree process, then given

the data, is again a Polya tree process. In particular, if is a Dirichlet process

with parameter then given the data, is also a Dirichlet process on

with updated parameter Also, from (7) under squared error loss,

the Bayes estimators of the conditional probabilities are given by

74
and

The posterior variance of the conditional probabilities are given by

Also, the Bayes estimator of the unconditional probabilities

and their posterior variances are given by

and

respectively.

ANALYSIS OF ARC 090 TRIAL DATA

As mentioned earlier, we have reduced 51-dimensional data to 17-dimensional

data by developing a weekly index of urine samples being positive or negative.

A week is considered to be negative for opiates if at least two observations in

this week are negative. Otherwise, the week is considered to be positive for

opiates. Clearly, this approach takes into account the censored observations,

We have denoted the positive weeks by 1’s and the negative weeks by 0’s. For

simplicity, we assume that the parameter of the Dirichlet process is given by

This corresponds to the Lebesgue measure on [0, 1].

Thus, for no sample case, the prior guess of the unconditional probability

is and that of the conditional probability The

corresponding Bayes estimates for some selected sequences

75
for the three treatments buprenorphine, methadone 20 mg, and methadone

60 mg are given by the columns 2 and 3 in tables 1, 2, and 3. For example, if

then from table 1 we observe that

= 0.37094907407 and = 0.9921996880.

Graphs of unconditional probabilities for some sequences (up to length five) for

the three treatments are given in figures 1, 2, and 3.

TABLE 1. Conditional and unconditional probabilities of some selected

sequences for buprenorphine treatment

76
The tables and figures show that for all the three treatments the probabilities for

consecutive positive weeks of a fixed length are larger than the probabilities of

any other sequences of the same length. The probabilities of consecutive

positive weeks for buprenorphine and methadone 60 mg are smaller than the

corresponding probabilities for methadone 20 mg.

TABLE 2. Conditional and unconditional probabilities of some selected

sequences for methadone 20-mg treatment

77
ACKNOWLEDGMENTS

Dr. Ram Jain of the Division of Medications Development, National Institute of

Drug Abuse made helpful comments. Also, Stavros Tourkodimitris, a graduate

student, helped with the calculations.

TABLE 3. Conditional and unconditional probabilities of some selected

sequences for methadone 60-mg treatment

78
FIGURE 1. Unconditional probabilities for buprenorphine treatment

FIGURE 2. Unconditional probabilities for methadone 20-mg treatment

79
FIGURE 3. Unconditional probabilities for methadone 60-mg treatment

REFERENCES

Basu, D., and Tiwari, R.C. A note on the Dirichlet process. In: Kallianpur, G.;

Krishnaiah, P.R.; Ghosh, J.K., eds. Statistics and Probability: Essays in

Honor of C.R. Rao. New York: North-Holland, 1982. pp. 89-103.

Billingsley, P. Probability and Measures. New York: Wiley, 1979.

Blackwell, D. Discreteness of Ferguson selections. Ann Stat 1:356-358, 1973.

Ferguson, T.S. A Bayesian analysis of some nonparametric problems. Ann Stat

1:209-230, 1973.

Ferguson, T.S. Prior distributions on spaces of probability measures. Ann Stat

2:615-629, 1974.

Ferguson, T.S.; Phadia, E.G.; and Tiwari, R.C. Bayesian nonparametric

inference. In: Ghosh, M., and Pathak, PK., eds. Essays in Honor of D. Basu

Vol. 17, IMS Lecture Notes - Monograph Series. Hayward, CA: Institute of

Mathematical Statistics, 1992.

Kraft, C.H. A class of distribution function processes which have derivatives. J

Appl Probability 1:385-388, 1964.

Metivier, M. Sur la construction de mesures aléatoirs presque súrment

absolument continues par rapport à une mesure donnée. Z.

Wahrscheinlichkeitstheorie view. Geb. 20:332-344, 1971.

80
AUTHOR

Ram C. Tiwari, Ph.D.

Associate Professor

Department of Mathematics

University of North Carolina at Charlotte

Charlotte, NC 28223

81
Three Estimators of the Probability of

Opiate Use From Incomplete Data

Alan J. Gross

INTRODUCTION

Drug testing in biologic fluids, especially urine, has become the usual method

by which addicts in a treatment program are evaluated to determine whether

they are adhering to the treatment regime in which they have been placed.

Unfortunately, issues such as sensitivity and specificity of the various tests have

caused difficulties in the past. The Council on Science Affairs (1987) has dealt

with these important issues.

Besides these issues of sensitivity and specificity, there are concerns about

whether a random time or a fixed time sampling scheme should be used when

collecting urine specimens from subjects who are involved in a clinical trial that

is designed to test the safety and efficacy of a new pharmocotherapy for

treatment of opiate dependence.

It is the purpose of this chapter to consider three estimators of the probability

that an addict tests positive for a particular opiate and compare these estimates

for the ARC 090 data that were generated by means of fixed time sampling.

The properties of these estimators will also be investigated, and some

preliminary results will be given. Although other important issues exist in this

area of research, such as random time sampling schemes, they are not

specifically addressed in this chapter.

ESTIMATORS OF THE PROBABILITY OF OPIATE USE

In an effort to estimate the probability of opiate use by an addict during the time

period in which he or she is enrolled in a clinical trial designed to reduce drug

dependence, the following assumptions and definitions are required.

Assume that an individual within a clinical trial is scheduled to present m times

for testing of the presence of the opiate for which he or she is being treated. On

82
the visit, the random variables and are defined as

and

the individual tests positive for the opiate,

the individual tests negative

the individual appears for the test and is still in the trial,

the individual does not appear

It is noted that m can and does change from subject to subject,

and in the data set that is considered when treatment groups are compared,

once a subject has been censored from the trial, that subject never returns for

any future testing. It is further assumed that

are Bernoulli random variables such that

(i)

in the first case

in the second case

(ii)

(2)

and in the third case, the correlation structure

(iii)

and

(b) are iid Bernoulli random variables such that

The three correlation structures considered here deal then, respectively, with

the following three scenarios:

83
1. There is correlation between all pairs of visits for a given individual. In this

case, the correlation between successive visits is assumed to be greater (in

absolute value) than visits that are more distant. The structure is the same

as in the simple autoregressive model.

2. The correlation in this case is assumed to stay constant between all pairs of

visits, successive as well as more distant, within an individual. This

assumption may tend to be somewhat conservative.

3. The correlation between successive visits within an individual is assumed

and is constant within individuals. It is also assumed constant from

individual to individual. However, more distant visits are assumed to be

uncorrelated.

The dependence or correlation structure presented in this chapter differs, to

some extent, from correlated binomial random variables that were considered in

other applications. These earlier applications include correlated binomial

models to predict the probability of rainfall on a given day realizing that the

occurrence or nonoccurrence of rain on a given day depends on the occurrence

or nonoccurrence on the previous day. Such models were developed by

Gabriel (1959), Gabriel and Neuman (1962), and Klotz (1973). In the model

considered by Klotz (1973), it can be shown that

As a second example in ophthalmology studies, a particular disease may be

present in one eye, both eyes, or neither eye in a patient. Rosner (1984)

considers a correlated binomial model in this situation because, clearly,

absence or presence of disease in the two eyes of an individual is not

independent from eye to eye. Finally, in this vein, Kupper and Haseman (1978)

and Haseman and Kupper (1979) apply correlated binomial models to analyzing

data within and among animal litters for which the responses are dichotomous,

e.g., occurrence or nonoccurrence of a malformation.

Consider now, the estimator for the probability of opiate use. Define as

This definition indicates that an individual who is never present for a test to

determine his or her drug abuse status is very likely, if not certain, to be still

84
abusing the drug. It should be noted that (1) this definition does not distinguish

all sequences, for example, it does not distinguish 000111 and 111000; and

(2) represents an average across visits for each individual. Although, these

are somewhat limiting, it is an initial attempt to deal with such binomial data in a

relatively simple manner.

The first principal goal of this chapter is to obtain and under the

three correlation structures as indicated by the three points listed above. This

constitutes the next section.

Define Then,

Now,

Furthermore,

where is the vector of the u-values obtained by the subject on his

or her -visits, 1. Thus, and

(5)

Derivation of Var( ) is considerably more complicated. Thus, some preliminary

considerations are in order prior to obtaining Var( ) for the three cases that are

dealt with in this chapter. Let the random vector be a single m dimensional

observation from a population whose cd is that is, is multivariate

in nature. Suppose, and let

and suppose, in total generality, E(Ui) = μi and Var Ui

 = =1, . . . , m.

Assume, further, a hypergeometric sampling process such that

are sampled from (U1, . . . ,Um), v m without replacement. Then if

we may rewrite where

(6)

The sampling process is assumed independent of U1, . . . , Um. That is,

85
Thus,

Hence,

(7)

Furthermore, I

2

(Ui) = I(Ui) since I(Ui) takes only the values 0 and unity; and

I(Ui)l(Uj) = 1 if both Ui and Uj are selected in the sample. Otherwise,

I(Ui)I(Uj) = 0. We note,

Finally, we obtain

Consider, again, the estimator for interest, i.e.,

(8)

( 4')

Recall, the three correlation structures among the of interest, i.e., (1), (2),

and (3).

86
In the first case, and corr(Ui

, Uj) =

. A useful result that is easily verified is

(9)

An application of (8) and (9) then yields

(11)

Unconditioning on V except requiring v 1 yields

(12)

In the second case, E(Ui) = p, Var Ui = pq and corr( ) =

.Thus, one can show, without difficulty,

(13)

Hence,

(14)

Finally, in the third case,

and corr(Ui, Uj) = 0, j > i + 1, i = 1, . . . , m - 2.

Here,

Define, generically, to represent Var( for all three

cases of interest. It then follows that, unconditionally,

(16)

87
Thus, to review, E( ) is given by (5) and Var( ) is given by (16).

It can be shown without much difficulty that if is given (12) or (15)

0 implying that is a consistent estimator of p assuming

1. On the other hand, if is given by (14), then consistency does not hold.

Finally, if is given by (12) it is noted that at p = 0,

(17)

(18)

it can be demonstrated with some difficulty that f(p) is an increasing function of

and so the bounds on Var( ) are

(19)

Consideration of is contained in the appendix. Finally, Mendenhall and

Lehman (1960) show that

and provides two significant figure accuracy for

COMPARISON OF TREATMENT GROUPS

The goal of this section is to develop a test of the hypothesis H0: pl = p2,

where piis the probability an individual in the treatment group tests

positively for the presence of the opiate. It is noted, in the example to be

presented in the next section, that there are three treatment groups in question;

therefore, multiple comparison methods are used in comparing the results

among the three groups. In this section, the notation adds subscripts to

represent the jth time the individual is tested within a treatment group.

Let be the proportion of the trials in which the individual tests positive on

the ith treatment, ni

. Then, it is clear from (4) that

(4')

88
Define Again, note that

(5')

since within each treatment group it is assumed pi1 = Thus,

(19)

If the same reasoning is followed concerning Var one finds

(16')

where, generically, are

stochastically independent for it follows that

It is easy to show that for all three cases, i.e., all three as

Thus, is a consistent estimator of where

In order to reduce the bias, let

is termed the reduced estimator and its realizations are presented as

reduced estimates in table 2, i = 1, 2, 3.

The variance of (21) can be approximated by the delta method. Thus,

(20)

(21)

(22)

89
Hence, to test for treatment difference, the following confidence intervals all at

( 1 /6) can be used:

(23)

where is the /6th percentile of the standard normal

pdf. Thus, confidence intervals for p1 – p2, p1 – p3, and p2 – p3 can be

constructed using (23) with overall confidence of at least (1 – ) .

ANALYSIS OF THE EXISTING DATA AND CONCLUSIONS

The methodology that has been developed in this chapter is now applied to the

double blind, three-armed controlled ARC trial. This trial was conducted to

evaluate the efficacy of buprenorphine (arm 1), methadone 20 mg (arm 2), and

methadone 60 mg (arm 3) in the treatment of opiate addiction. Data on only the

first 17 weeks of the study were used to study how well the patients were

maintained on the treatment drug. No analysis was performed on weeks 18

through 27.

Table 1 shows the summary results for the three treatment groups.

The correlation coefficient in each treatment group was estimated as an

average (unweighted) of the serial correlations for the patients in that group. It

should be noted from table 1 that there is no statistically significant difference

among the ’s. That is, roughly 77 percent of all individuals presented urine

samples in the first 17 weeks of the study. Furthermore, it can also be shown

that all three of the correlation coefficients are not statistically significantly

different from zero. However, it was decided to use the established values of

for illustrative purposes.

TABLE 1. Estimates of p, 

Treatment Group n

Buprenorphine 0.483 0.773 0.087 53

Methadone 20 mg 0.687 0.767 0.013 55

Methadone 60 mg 0.564 0.786 0.133 54

90
TABLE 2. Estimates of the probability of opiate use

Treatment Group

Buprenorphine (raw) 0.483 3.83 10-4 6.76 10-4 3.33 10-4

Methadone 20 mg (raw) 0.687 3.80 10-4 4.15 10-4 3.51 10-4

Methadone 60 mg (raw) 0.564 4.79 10-4 9.05 10-4 4.16 10-4

Buprenorphine (reduced) 0.468 4.05 10-4 7.08 10-4 3.52 10-4

Methadone 20 mg (reduced) 0.685 3.87 10-4 4.22 10-4 3.57 10-4

Methadone 60 mg (reduced) 0.558 4.90 10-4 9.25 10-4 4.26 10-4

Table 2 provides the raw and the reduced estimates of = 1, 2, 3, the

probability of detecting the opiate in each of the three treatment groups. Also,

the three estimates of variance are provided for the three different patterns of

correlation that are assumed.

Where assumes visits and have correlation assumes

all visits, adjacent as well as nonadjacent, have correlation and, finally,

is such that adjacent visits have correlation and nonadjacent visits have

correlation zero.

Overall, 95 percent confidence intervals for = 1, 2, 3 are then

easily obtained for each pair of treatment differences. The formula used is

to ensure an overall 95 percent confidence, = 1, 2, 3, the three variance

estimates based on the three correlation patterns assumed. Note that

= 2.409.

As one would expect, the largest variance occurs when is constant across all

visits, has a value between the smallest and largest values when visits and

have correlation and is smallest when adjacent visits have correlation

and nonadjacent visits have zero correlation.

If one examines the confidence intervals that are generated from table 2 (see

table 3) it is clear that buprenorphine is superior to methadone 20 mg,

regardless of the correlation pattern assumed. Furthermore, methadone 60 mg

is clearly superior to methadone 20 mg. However, it is still not clear that

buprenorphine is a better treatment regime than methadone 60 mg. However,

the analysis is suggestive of this conclusion, since the only situation where the

confidence interval contains the null hypothesis is when the correlation between

91
TABLE 3. Confidence intervals of the difference of the probabilities of opiate

use

Group Difference

Meth 20 - bup (raw) 0.137-0.271 0.124-0.284 0.141-0.267

Meth 20 - meth 60 (raw) 0.052-0.194 0.036-1.210 0.056-0.190

Meth 60 - bup (raw) 0.010-0.152 -0.014-0.176 0.015-0.147

Meth 20 - bup (reduced) 0.149-0.285 0.136-0.298 0.153-0.281

Meth 20 - meth 60 (reduced) 0.056-0.198 0.039-0.215 0.060-0.194

Meth 60 - bup (reduced) 0.018-0.162 -0.007-0.187 0.023-0.157

pairs of visits remains constant over all pairs of visits. If, however, this is the

situation, then mathematically random testing vs. systematic testing does not

make a great deal of difference, since fixed as well as randomly spaced times

between visits will have the same correlation.

It should be noted at this point that the true correlational structure between pairs

of visits does not and should solely determine whether random or systematic

testing is appropriate. If the sampling scheme is determined on the basis that

an individual is still using a given substance during a given week or throughout

the study period, then random sampling is likely appropriate to detect his or her

use. However, if the extent of drug abuse is of importance, such as with the

ARC 090 study, then capturing all the episodes of drug abuse is important and,

hence, systematic sampling is likely to be more useful since drug-seeking

behavior is not random. Finally, it is noted that carryover effects are probably

quite important but are not considered here.

APPENDIX

Theorem: Suppose

Proof: f(0) = 0 is trivial. To find f(1) an application of L’ Hôpital’s rule twice

is needed. Finally, to show f(p) increases in it is noted that

92
Thus,

The denominator is positive for 0 < < 1 since m(1 - p) > 1 –

m

for in this

domain. This is easily established by induction on m.

Finally, it is necessary to establish that

(A.3)

for m > 1 and 0 1. If g( ) is defined as

(A .4)

then g(0) = m – 1 and g(1) = 0. To complete the establishment of (A.3), it

suffices to show g( ) is monotone on 0 1. To this end,

for 0 1, which completes the demonstration.

ACKNOWLEDGMENTS

The author acknowledges the following colleagues for their assistance in the

preparation of this chapter: Hurshell H. Hunt and Philip F. Rust at the Medical

University of South Carolina for their discussions in the development of the

estimators presented herein; Carol K. Redmond and Mei-Ling Lee at the

University of Pittsburgh and Harvard University, respectively, for their reading of

the initial draft and their comments, which have been incorporated in this

revision and which have improved it substantially; Kuo-Chang Wang, graduate

student at the Medical University of South Carolina, who helped the

computations that were performed; and Ram B. Jain, who made comments on

the original draft that have been included in this version.

REFERENCES

Council on Science Affairs, Scientific issues in drug testing. JAMA

257(22):3110-3114, 1987

Gabriel, K.R. The distribution of the number of successes in a sequence of

dependent trials. Biometrika 46:454-460, 1959.

Gabriel, K.R., and Neuman, J. A Markov chain model for daily rain-fall

occurrence at Tel-Aviv. Q J Roy Meteorol Soc 88:90-95, 1962.

93
Haseman, J.K., and Kupper, L.L. Analysis of dichotomous response data from

certain toxicological experiments. Biometrics 35(1):281-293, 1979.

Klotz, J. Statistical inference in Bernoulli trials with dependence. Ann Stat

2(1):373-379, 1973.

Kupper, L.L., and Haseman, J.K. The use of a correlated binomial model for the

analysis of certain toxicological experiments. Biometrics 34(1):69-76, 1978.

Mendenhall, W., and Lehman, E.H. An approximation to the negative moments

of the positive binomial useful in life testing. Technometrics 2:233-239, 1960.

Rosner, B. Multivariate methods in ophthalmology with application to other

paired-data situations. Biometrics 40(4):1025-1035, 1984.

AUTHOR

Alan J. Gross, Ph.D.

Professor

Department of Biostatistics, Epidemiology, and Systems Science

Medical University of South Carolina

171 Ashley Avenue

Charleston, SC 29425-2503

94
Summary of Discussion: “Three

Estimators of the Probability of Opiate

Use From Incomplete Data” by Gross

Ram B. Jain

Dr. Redmond, who reviewed Dr. Gross’ chapter prior to the technical review

meeting, questioned the appropriateness of the assumption that data are

missing at random. Dr. Gross agreed that this assumption may not be

appropriate and that further work needs to be done in this area.

Dr. Fisher warned against jumping to conclusions too soon even if the

missing value and/or dropout rates are the same across different treatment

groups. In the placebo group, for example, patients may miss visits and/or

drop out because of the lack of efficacy, whereas in the other groups, they

may miss visits and/or drop out because of adverse events. These different

reasons for the same missed visits and/or dropout rates must have a bearing

on the inference that is drawn and must be carefully looked into since they

may have different implications for different treatments.

Dr. Redmond also raised the issue of using an estimator in which one looks

at the average of visits across time. Two treatments might result in the same

average across visits over time, but for example, positive urines may be

clustered at the end of the visits in one case and toward the beginning or

scattered throughout in the other case. An estimator that looks only at the

average across visits over time would not be able to discriminate this different

pattern of positive urines over time in the two treatments.

I suggested that a model be considered that incorporates possible different

correlational structures for different segments of the study. The addicts do

not suddenly stop abusing the drugs, because drug abuse medications take

time to work. During the first segment of the study, there probably will be

longer sequences of positive urines with occasional negative urines. This

will be followed by a probably random pattern of negative and positive urines

indicating the medication has started working. During the last segment of the

study, if the medication did work, there probably will be longer sequences of

95
negative urines with occasional positive urines. Dr. Gross indicated that such

a model may be possible if a close form variance estimator can be obtained; for

example, different correlational structures suggested by him in his chapter can

be used for different Segments Of the study or a piece-wise fitting Of the data

can be attempted (see Weng, this volume).

Dr. Hedayat suggested that the patient characteristics, for example, sex or age,

be included in the model rather than reduce the problem to only a few factors,

that is, p’s, and p’s as in Dr. Gross’ chapter. One of the participants also

suggested that visit number be used as a covariate since the probabilities of a

positive urine are likely to change over time.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

96
Issues in the Analysis of Clinical Trials

for Opiate Dependence

Dean Foilmann, Margaret Wu, and Nancy Geller

INTRODUCTION

The analysis of clinical trials of opiate dependence presents special challenges.

In particular, the amount of missing data tends to be substantial. In trials of

cardiovascular disease, dropout rates higher than 5 percent per year are

considered high. In contrast, in a recent trial of three treatments for heroin

addicts, ARC 090, more than two-thirds of the patients dropped out by the end

of 17 weeks. In such a trial, any pronouncement of treatment efficacy depends

on how one deals with missing data.

There are two main possibilities for dealing with missing endpoint data in a

clinical trial: ignoring them or using imputation or modeling. Ignoring the

missing data can lead to bias in inference if the data are not missing at random

and can violate the intent-to-treat principle, which demands that all subjects be

analyzed as part of the treatment group to which they were randomly assigned.

Imputation or modeling is inherently assumption dependent but can provide

accurate answers if the assumptions are met. A problematic feature of opiatedependence trials is that some assumptions are completely uncheckable. In

essence, a guess is made about drug use on days of missed visits. Although

the guess can be based on other data or informed opinion of observed

behavior, the degree to which the guess reflects unobserved behavior is

unknowable.

Wu and Carroll (1988), Wu and Bailey (1989) and Wu and colleagues (1991)

considered the effect of censoring when comparing changes Of a continuous

response variable between treatment groups. They used the term “informative

censoring” when the probability of a missing data point depends on the

parameter of interest. They showed that, when the censoring is informative,

falsely assuming random censoring could give biased estimates of the group

slope means and the between-group differences. Statistical procedures to

account for informative censoring were also proposed.

97
This chapter discusses different methods of dealing with longitudinal data with

many values missing. It is assumed that individuals are supposed to be tested

at a fixed number of times (e.g., Monday, Wednesday, and Friday of each week

for 17 weeks) and that each test is either positive, indicating drug use, or

negative, indicating nonuse. However, because some individuals do not show

up for some tests, the test value for that visit is missing. For simplicity, the

authors’ primary method of analysis will compute a summary measure of each

individual’s sequence of tests and compare these measures between the two

groups.

A second section of this chapter considers different methods of imputation and

modeling for these data, which are considered to be binary repeated

measurements. Notation is developed and the case of no missing data

discussed. Ad hoc tests for missing data are explored, followed by the simple

approach of imputing a specific value to all missing observations. Combining

test statistics for treatment efficacy and equal missing data is considered. Next,

models for informative censoring are introduced whereby individuals’ imputed

values depend on their observed data. This generalizes previous work to the

case of binary data. Section three applies some of these methods to the data

of ARC 090. The discussion section suggests some tests for more complicated

null hypotheses.

NOTATION

The authors assume that the subjects are randomly assigned to one of two

treatment groups with subjects in group k = 1,2. The data of interest consist of

the repeated binary measurements where

In the background, we imagine a population of vectors that govern

the response of the ith subject in the kth group. These vectors are paired with

subjects via the randomization process. For notational convenience, we define

Because subjects can miss visits as well as drop out of the study, define

98
Similar to the notation, let We also define, for the ith subject

in the kth group, the last visit number and mjk as the number of available

test results.

For simplicity, it is assumed that the hypothesis of interest is whether the

average differs between the two groups, A useful notation for this is

where the expectation is over the subscripts (here i and j).

Note that each subject is allowed a different average response proportion and

response proportions are averaged over time. The probability of a positive

response within a subject over time may or may not be the same. With no

missing data, a reasonable test of is the standardized difference in the

mean proportion of positive tests of the two samples

where is the proportion of positive tests for the ith subject in the kth group,

and

(2)

where the average of the

Alternately, may be taken as the pooled sample estimate of the variance.

With either estimate of variance, T1 has an asymptotic standard normal

distribution. Another reasonable test in this situation is the two-sample

Wilcoxon test.

AD HOC TESTS WITH INCOMPLETE DATA

If some of the tests are missing, (1) may require modification. Suppose that

that there is no variation in the probability of a positive test over

time), but again different subjects are allowed different positive propensities.

Implicit in this formulation is that the observable data on an individual reflect the

unobservable data on that individual. Note, however, that these assumptions

do allow for a dependency between the probability of a missing test and the

probability of a positive response. An unbiased estimate of an individual’s

here is the average response on completed visits or A simple

way to compare these proportions in the two groups is to use (1) with a modified

variance estimate. In effect, the authors are comparing the unweighted

within-group averages and testing a new hypothesis

99
A consistent variance estimate can be derived under the assumption

Since the are allowed to vary within each group, a random effects model is

specified for the for each k. The mean and variance of are denoted by

The following expectations can be used to provide simple method-ofmoments estimates of

where The last two equations can be used to estimate

Under the random effects model,

and an estimate of can be gotten by estimating

With missing data, the denominator of (1) is then estimated by the square root

of Call this test T2

.

One variation on this theme is to use a weighted comparison of the average

responses where is weighted by mik. However, this weighted analysis

requires the stronger assumption that the probability of missing a visit or

dropping out is unrelated to a person’s average response. If persons who drop

out early have a higher proportion of negative tests, the weighted estimate will

tend to be biased downward. However, if the additional assumption is

warranted, the weighted analysis can be more efficient than that based on the

unweighted average.

Another method is to calculate ranks based on the and to perform a rank

test. This approach is appealing since it is based directly on the unbiased

response averages for each subject, Furthermore, ranks tend to dampen the

influence of the more variable based on few observations (Wu et al. 1991).

Suppose the proportion positive is ranked from lowest to highest. Tied

observations can be resolved by evaluating the number of complete

100
observations and whether the ties are above or below the overall mean

I f

Rank If the equal sample averages are below the overall mean, take

Treating ties in this manner is consistent with the

ranking based on the shrinkage or Empirical Bayes estimates of the This

generalizes a method for breaking ties suggested by Sahlroot and Pledger

(1991). Call this rank test T3.

The assumption that may be untenable. For example, the chance of a

positive test may increase as the study progresses and subjects lose interest.

Even in this case, the subject average provides an unbiased estimate of his

or her average over the complete visits. Therefore, tests of the hypothesis

that

can in principle be made by looking at either the ranks of the or the

difference of the unweighted within-group averages. One problem with the

former test is that a variance estimate requires additional structure to be put on

the Although the test based on ranks can be used in a straightforward

manner, may be of limited interest if the distribution of the differs from

that of the For example, if increases with j for both groups and subjects

drop out early for one group, the group with the earlier dropouts will tend to

have a lower test average. The test statistic could identify the better treatment

as the one with the earlier dropouts even if later were higher for the group

with earlier dropouts.

Since the rank test of may result in a misleading inference, it is necessary

to examine whether the missed visits and dropout times differ between the two

groups. Tests of equality of the pattern of missingness between the two

groups should be calculated. Rank tests, tests of means, or logrank tests

could be used. Informally, these tests could be used to see how meaningful

the test of is. For example, if a similar pattern of missingness is expected

to occur over time in the treatment groups, one could use a test of the

difference in proportions of missing data in the two treatment groups, which is

analogous to (1) with replacing and a suitable estimates of variance, say

replacing Call this test statistic M1. A Wilcoxon test based on is

also considered; call this test statistic

101
More formally, a test for missingness can be combined with a test of efficacy

using a multivariate test (O’Brien 1984; Pocock et al. 1987). Here the null

hypothesis is

and the alternative is

that is, one treatment is better than the other with respect to both the proportion

of positive tests and the proportion of missing tests.

As an example, consider combining two rank tests, such as T3 and M2. O’Brien

(1984) proposed ranking each outcome separately, as one would to perform a

Wilcoxon rank sum test on each outcome and summing the ranks over the two

outcomes, He then proposed calculating a Wilcoxon rank sum test for these

sums. Call the resulting statistic 0,. In the case of more than two samples,

O’Brien suggested ranking each outcome over all samples, forming the rank

sums for each subject, and then using one-way analysis of variance on the

sums. Alternatively, a Kruskal-Wallis test could be used on the sums.

More complex combinations of test statistics may be formed using the method

proposed by Pocock and colleagues (1987). To combine T2 with M1in an

O’Brien-type statistic, the correlation between T2 and M1 would need to

be estimated. Pocock and colleagues (1987) gave an explicit reduction of the

formula for O’Brien’s generalized least-squares statistic when endpoints are

equally correlated and the within-group data are iid. The within-group data here

are not iid, however, since the variance of depends on Estimation of the

correlation between these test statistics requires further work.

SIMPLE IMPUTATION

If the assumption that is untenable, an imputation of a specific value for

each missing data point may be reasonable. We will call this simple imputation.

One possibility is to replace missing responses with positive responses. This is

appropriate if it seems likely that subjects would have tested positive if they had

102
been tested. Another rationale for this imputation is that it defines a new

endpoint: missed test or positive test. This endpoint tests a new hypothesis

where is the probability that the ith person in the kth group is positive or

missing for the jth test. One could argue that both positive tests as well as

missing data suggest failure of the program. An advantage of the simple

imputation approach is that the analysis then proceeds as if complete data had

been obtained, and (1) or its rank analog can be used. The test statistic T4is

referred to as (1) with a value 1 imputed for missing values.

MODEL-BASED IMPUTATION

The basic idea here is to use a model to provide an accurate test of the original

hypothesis even if individuals likely to test positive tend to

drop out or if The authors attempt to succinctly describe for each

group with a model, estimate the parameters of the model separately in each

group, and then compare the estimate of to the estimate of

Although this approach is heavily model based, one can allow

for quite general effects of dropping out, missed visits, and other factors as long

as they are correctly incorporated into the model.

To justify our procedure in a simple setting, ignore the treatment identifier k and

suppose that the following model holds:

(4)

(5)

where is a random parameter with some distribution H with mean zero, and

B, are fixed-effects parameters. In other words, each subject draws a

random propensity for a positive test, ßoi, from H, which also affects the

probability of a missed visit. If is not zero, the missing observations are said

to be informative with respect to the parameter of interest, (Wu and Carroll

1988).

103
Although maximum likelihood estimation could be performed using the

a simpler approach can be argued as was done by Wu and Bailey (1989).

Suppose the are ignored. The model defined by (5) can be viewed as an

Empirical Bayes model. The information from the ith individual is given by

or equivalently mi since For the ith individual and any

prior H, the posterior expectation is increasing (decreasing) as a

function of mi when a, is negative (positive). A proof of this result is presented

elsewhere. In other words, if is positive, individuals who are likely to test

positive are also likely to miss tests.

This result suggests that a simple way to capture the information contained in

is to use the model

where has a distribution H( ) with mean 0, and h( ) is some function that is

allowed to be either increasing or decreasing, such as a polynomial, perhaps

with restricted coefficients.

The above argument justifies fitting a logistic regression model with random

subject effects and other fixed effects that describe the missingness. Such

models have been discussed in a more general setting by Pierce and Sands

(1975), Stiratelli and colleagues (1984), and Follmann and Lambert (1989). The

approach of Follmann and Lambert (1989) is used and H is estimated via

nonparametric maximum likelihood, along with parametric estimates of the fixed

effects. Under this approach, H is assumed to follow a distribution with a finite

number of support points. The number of support points is estimated by the

data.

For the problem at hand, consider the following model:

for k = 1,2. Note that the probability of a positive response is assumed free of j

and the test derived from it is appropriate for the hypothesis

Therefore, results from this procedure can be compared with other tests of the

same hypothesis from the previous sections.

104
The numerator of the model-based test statistic is

where the expectations are Empirical Bayes posterior expectations using the

within-group estimates of the random effects distribution, the fixed effects, and

each individual’s data. The asymptotic variance of this test statistic can be

estimated by the delta method, given a covariance matrix for the estimates.

The authors use the observed Fisher Information (pretending that the number of

support points is known) to estimate this covariance (Follmann and Lambert

1989).

In general, trends in the could be made to depend on j via a covariate, for

example, polynomials of j or Iog(j). If the depend on j and this dependence

is accurately summarized via the random effects model, the original hypothesis

can be tested, even with missing data.

EXAMPLE

A recent randomized clinical trial compared three treatments-buprenorphine,

methadone at 20 mg (methadone 20), and methadone at 60 mg (methadone

60)-for their ability to reduce opiate use within a group of addicts. This section

focuses on the buprenorphine and methadone 20 groups.

Respectively, 53 and 55 subjects were randomized to these two groups. The

methadone 60 group contained 54 subjects. Following randomization, urine

tests were conducted three times per week for a total of 17 weeks. One subject

was assigned to the buprenorphine group who never took a test. Although one

might include this subject with some imputed value in an analysis of the

treatments, she is excluded for simplicity.

Figure 1 displays the proportions of positive tests over visits for the two groups.

Buprenorphine is almost always better, and there seems to be little trend in the

proportion positive. Figure 2 displays the proportion of missed tests over time.

Both groups show increasing trends that seem fairly comparable. Figure 3

displays the scatter plot of that is, the proportion positive vs. the

proportion missed for the two groups. A moderate positive correlation = .51)

is seen between the two in the buprenorphine group, whereas the correlation is

less strong in the methadone 20 group Also note that subjects in the

buprenorphine group who always test positive have many missed tests. Some

subjects in the methadone 20 group who always test positive rarely show up.

105
FIGURE 1. Proportion of positive tests over time, by treatment

Table 1 shows some sample statistics for the two groups. Burprenorphine has

a lower average response proportion, a larger random-effects variance, and

also a larger variance of The latter discrepancy is influenced both by the

larger and the average response being closer to .5 for the buprenorphine

group. The average proportion missing is somewhat larger in the methadone

20 group.

Table 2 provides the results for the various tests discussed in the text. For all

test statistic numerators, the methadone group result is subtracted from the

buprenorphine group result. The first two tests provide very similar results for

the hypothesis that the average is the same for the two groups. The first test

is obtained from the results of table 1. Both tests indicate that the

buprenorphine group has a substantially lower probability of a positive test.

For the rank test, the authors determined the number of times that the Empirical

Bayes approach adjudicated tied observations. With no ties, each of the 107

observations forms a “cluster” of 1. For these data, there were 69 clusters,

ranging in size from 2 to 25. For example, for there are four

observations, one with mi = 4 in the buprenorphine group and 3 in the

106
FIGURE 2. Proportion of missed tests over time, by treatment

methadone 20 group with mi = 4, 2, and 2. For 1.0, there were 25

observations. Following the Empirical Bayes method of breaking ties, there

were 92 clusters. Interestingly, when the ties are not broken, the Wilcoxon rank

test is -2.85. Thus, how ties are treated makes a difference here.

Although the overall proportion missing is somewhat higher in the methadone

group, a test of the difference in these proportions is not significant. However,

this difference explains why the test statistic that imputes 1 for missing

observations is higher than the analogous test without imputation.

Burprenorphine is better both with respect to missing data and with respect to

the proportion of positive tests.

The O’Brien rank test shows that buprenorphine was better than methadone 20

simultaneously with respect to efficacy and missingness. In calculating this

statistic, average ranks were used for ties. The final ranking had 80 clusters, 1

of size five, 4 of size three, and 15 of size two. It is not surprising that the value

of this test statistic is smaller in absolute value than the rank test for the

107
FIGURE 3. Proportion of positive and missed tests, by subject

proportion of positive tests. The difference in proportions of missingness,

although not significant by itself, has a modest diluting effect.

The test based on the model for informative censoring provides the smallest

p-value of all tests of the hypothesis It is substantially larger

than the test based on the This is not surprising since tests that require

more assumptions are generally more efficient.

The estimated models for the two groups are presented in table 3. Using the

Wald statistics, the missing data are seen to be highly informative for the

methadone 20 group and not as informative for the buprenorphine group. Since

subjects with fewer missing observations tend to drop out later, it is somewhat

misleading to talk about the separate effects of mi and Li. However, note that

for the methadone 20 group, subjects with larger mis (i.e., fewer missing

observations) tend to have a lower proportion of positive tests. Subjects who

drop out later are more likely to test positive.

108
The estimated average proportion of positive tests for the two groups in table 3

is quite close to the average of the c,s. However, the variance of is

substantially smaller than from table 1. As mentioned previously,

the smaller variability is not surprising since the model introduces more

“structure” to the data. However, the ratio of the estimated variances is similar

for the two approaches.

For simplicity, detailed comparison involved two groups. Finally, the authors

use an evaluation of the three arms using the O’Brien rank test, which

simultaneously tests equality of efficacy and missingness over all three arms.

The Kruskal-Wallis chi-square test with two degrees of freedom had the value of

8.55 (p=.01). We then considered the three pairwise comparisons and used a

Bonferroni correction to determine an (approximately normal) critical value of

2.39. Buprenorphine is better than methadone 20 (01 = -2.70), but not better

than methadone 60 (01 = -.95). Methadone 60 was better than methadone 20,

but not significantly so (01 = 2.15).

TABLE 1. Some summary statistics for the buprenorphine and methadone 20

groups

Group

Statistic

Buprenorphine

(n=52)

.49

.11

.0025

.48

.1163

Methadone 20

(n=55)

.69

.07

.0016

.58

.1119

109
TABLE 2. Tests comparing the response proportions between the

buprenorphine and methadone 20 groups

Test

Difference in average with

random effects variance

Hypothesis Z Value

-3.05

Rank version of above with Empirical -3.01

Bayes adjudication of ties

Difference in average -1.63

Difference in average with missing -3.48

to 1 imputation

O’Brien’s rank test -2.70

Difference in average -3.82

TABLE 3. Parameter estimates for the models of informative censoring. The

estimated mixing distribution for the buprenorphine (methadone

20) group had 4 (2) points of support. Estimated Wald statistics

are provided in parentheses.

Effect

Sample variance of

Group

Buprenorphine

1.20

Methadone 20

-.022

(-1.29)

-.021

(-1.14)

.48

.00133

.38

-.136

(-6.14)

.131

(5.59)

.68

.00116

110
DISCUSSION

This chapter briefly introduces and illustrates several techniques that may be

useful for dichotomous repeated measures with a substantial proportion of

missing data. A more rigorous evaluation would be useful before definitive

recommendations are made. Nonetheless, several points can be offered.

The rank test with Empirical Bayes adjudication is an appealing procedure

because it allows an unbiased robust comparison of two proportions as long as

it is assumed that the probability of a positive test does not vary with j. The

analogous test of means may be more substantially affected by based on

few observations. Furthermore, the means test requires some structure to

derive a variance estimate.

The simple imputation of missing to positive might be favored either if one felt

that subjects were taking drugs on missed days or if a combined endpoint were

thought reasonable.

The attraction of the model-based approach is that, in principle, it can provide a

test of the original hypothesis. The disadvantage to this approach is in the

implementation. Issues of covariate selection and model fit need to be

explored. Additionally, optimization requires some care due to the possibility of

local maxima and numerical stability. For example, in the methadone 20 group,

it seemed that an additional support point at would slightly increase the log

likelihood. However, this point was not included due to numerical problems with

the information matrix.

In general, there may be additional information to aid investigators in deciding

how to deal with each specific missing datum. For example, some missing data

might correspond to occasions when the subject was strongly suspected of

using opiates. Such additional information can be incorporated into a

combination procedure in which the imputation from missing to positive is made

for a subset of the data. The other procedures discussed in this chapter could

then be applied to the partially transformed data. However, it is important to

recognize that no statistical procedure will improve the results from a trial with

more than two-thirds of the endpoint data missing. Ultimately, the quality of

evidence from such a trial is more like that of an observational study.

111
REFERENCES

Follmann, D.A., and Lambert, D. Generalizing logistic regression by

nonparametric mixing. J Am Stat Assoc 84:295-300, 1989.

O’Brien, P.C. Procedures for comparing samples with multiple endpoints.

Biometrics 40:1079-1087, 1984.

Pierce, D.A., and Sands, B.R. Extra-Bernoulli Variation in Binary Data.

Technical Report 46. Corvallis, OR: Oregon State University, Department of

Statistics, 1975.

Pocock, S.J.; Geller, N.L.; and Tsiatis, A.A. The analysis of multiple endpoints in

clinical trials. Biometrics 43:487-498, 1987.

Sahlroot, J.T., and Pledger, G.W. “Monitoring Plasma Levels in Response to

Monitored Plasma Concentrations: Can Unblinded Staff Adhere to Objective

Criteria?” Unpublished manuscript, 1991.

Stiratelli, R.; Laird, N.; and Ware, J.H. Random effects models for serial

observations with binary response. Biometrics 40:961-971, 1984.

Wu, M.C., and Bailey, K.R. Estimation and comparison of changes in the

presence of informed censoring: Conditional linear models. Biometrics

45:939-955, 1989.

Wu, M.C., and Carroll, R.J. Estimation and comparison of changes in the

presence of informative censoring by modeling the censoring process.

Biometrics 44:175-188, 1988.

Wu, M.C.; Hunsberger, S.; and Zucker, D. Comparison of changes in the

presence of censoring: Parametric and nonparametric methods. In:

Proceedings of the Biopharmaceutical Section of the American Statistical

Association. Alexandria, VA: American Statistical Association, 1991, pp. 291-

299.

ACKNOWLEDGMENTS

Dr. Ram B. Jain provided the data; Mario Stylianou prepared the figures and

analyzed some of the data; and Dr. Jack C. Lee reviewed the manuscript and

provided useful comments.

AUTHORS

Dean Follmann, Ph.D.

Mathematical Statistician

Margaret Wu, Ph.D.

Mathematical Statistician

112
Nancy Geller, Ph.D

Chief

Biostatistics Research Branch

National Heart, Lung, and Blood Institute

National Institutes of Health

Federal Building, Room 2A-11

Bethesda, MD 20892

113
Summary of Discussion: “Issues in

the Analysis of Clinical Trials for Opiate

Dependence” by Follmann, Wu, and

Geller

Ram B. Jain

Dr. Jack C. Lee of the National Institute of Child Health and Human Development,

National Institutes of Health, who reviewed this paper, expressed concern about

the missing-at-random assumption implicitly made by the authors in some

of the models used by them. The same concern was expressed by many other

participants at one time or another. The assumption of missing at random is

questionable since a missed visit might be dependent on opiate abuse during

the days just prior to missed visits. Dr. Follmann replied that the model-based

imputation method presented by him did not require the assumption of missing

at random. The parameters a0 and a1 will be zero if the data are missing at

random.

I believe the distinction between a missed observation and a censored

observation was lost during this discussion. An observation is considered to

be censored when a subject permanently drops out of the study. For the

censoring to be informative, total experience or abuse history of the subject till

the time of censoring should play a role and should be investigated. A missed

observation, on the other hand, is a temporary event. For a missed observation

to be informative, a single or only a few events just prior to the missed visit

should play a role.

Dr. Lee also made a number of other suggestions that can be incorporated

in the models to describe the phenomenon of drug addiction. He suggested

that cyclic effects introduced by, for example, the pattern of drug abuse and

their relationship with missed visits can be incorporated in the models, and

the covariates that may affect bijk should be included in the models. He

suggested that the whole patient population may be divided into four or five

relatively homogeneous strata, and these strata can then be separately

analyzed. These analyses may not need the assumption of missing at

114
random. Dr. Lee was also of the view that the total study, for example,

may be divided into three periods and that each of these periods may be

studied separately. This might help in studying the issue of compliance.

Finally, he thought a goodness-of-fit test was lacking from the presentation.

There was a rather involved discussion about imputation of missing values

and the effect this may have on the inferences that are drawn. Dr. Hedayat

was concerned about always imputing missing observations to a single value.

Variations in patient characteristics across different areas may justify imputation

to different values. Dr. Wright was concerned about one treatment being

favored over another because of the specific imputation procedures used by the

statistician. Dr. Fisher was in favor of some kind of sensitivity analysis where

missing observations are imputed to different values in different treatment

groups to describe various possibilities under a different set of imputed

observations. However, Dr. Geller was of the view that you may come up

with any conclusion when the missing (censored) data are as massive as in

drug abuse trials.

Another suggestion was to consider some of the multiple imputation procedures

used by Dr. Don Rubin, Harvard University. This might give a handle on the

variability induced by the imputation procedure itself. It was pointed out that

one of the natural sets to select for multiple imputation would be the entire

history of the patient,

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

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Analysis of Clinical Trials for

Treatment of Opiate Dependence:

What Are the Possibilities?

Ram B. Jain

INTRODUCTION

One of the major primary outcome variables in clinical trials for treatment

of opiate dependence is the frequency of drug abuse, that is, of opiates

(primarily heroin), after therapy for opiate dependence has been initiated.

Because the episodes of opiate abuse are not directly observable, an estimate

for the frequency of opiate abuse is obtained from the urine samples collected

with a prespecified frequency and tested for the presence of opiates and their

metabolites. Hence, a data sequence of binary numbers for each addict is

available for analysis. Analyses of these data present serious obstacles.

To obtain the “true” estimate of the frequency of opiate abuse, it will be

necessary that each positive urine sample represent an independent episode

of opiate abuse. However, depending on the amount of opiate consumed

by an addict during a given episode, it will not always be true. Two or more

consecutive positive urine samples may represent the same episode of opiate

abuse. In other words, there is a probability that treatment effect will be

confounded with the carryover from one positive urine to another. It is difficult

to estimate carryover, because the probability of carryover for a given addict

varies from day to day and among addicts from one addict to another because

of differentials in drug-seeking behavior. Consequently, using the available

information on the kinetics of opiates, the frequency of urine samples is

selected in such a way that the probability of carryover is minimized and the

probability of being able to detect an episode of opiate abuse is maximized;

note that the probability of carryover is not entirely eliminated. This is the first

obstacle in analyzing these trials.

In clinical trials among drug addicts, the dropout rate is unavoidably high, to

the order of 80 percent in a placebo group. Also, even during the period the

addicts stay in the trial, they miss about one in every five scheduled visits for

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treatment. Hence, the number of missing or censored data points may be as

much as or more than the number of available data points, which reduces the

power of the statistical tests of hypotheses.

In 15- to 20-week trials, urine samples may be collected up to three times a

week. Hence, each addict may have 50-or-so data points for analysis. As

such, the problem of analyzing these trials may be perceived as a 50-or-so

dimensional problem. The selection of a powerful statistical method that will

permit 50-or-so dimensions with sample sizes on the order of 150 to 500

patients with substantial missing data to detect “true” treatment differences

is a serious challenge.

Before the possibilities for analyzing these data are considered, it would be

beneficial to understand the nature of treatment for opiate dependence.

Agonist therapy for opiate dependence essentially constitutes replacing the

abused opiate with another, most likely a synthetic opiate (called an opiate

agonist or an opiate partial agonist), with relatively less potential for abuse.

In replacement treatment, the next dose is given when the effect of the previous

dose is about to wear off. If the next dose is not given in time, the addict is

more likely to go out and seek the illegal drug of abuse. Overdosing amounts

to exposing the addict to the addictive potential of the replacement opiate.

Hence, each dose of the replacement opiate has its own pharmacological

effect and may be considered as one unit of treatment.

According to Blaine and colleagues (1981), replacement therapy “is intended

to . . . achieve a more pharmacologically stable physiological state.” Each unit

of replacement therapy, if successful, should lead to a physiological state that

is pharmacologically more stable than with the previous unit of replacement

treatment. Hence, attainment of a fully pharmacologically stable physiological

state at which the addict does not seek the abused opiate and is ready for

detoxification is going to be a gradual, one-step-at-a-time process.

WHAT ARE THE POSSIBILITIES?

Let be the probabilities (table 1) of an addict using the

abused opiate before entering the trial (i = 0) and after scheduled dose i (i > 0)

of the replacement opiate j. If each unit of the replacement opiate is

consistently successful and has no “reverse” therapeutic effect, P(i+1)j Pij,

i = 0, . . . . m - 1. However, because of missed doses and other factors, Pij can

assume any value between 0 and 1. Also, a data point s after scheduled dose

s, s = 2, . . ., m, for a given addict may not be available because of the missed

dose s or because he or she dropped out of the trial after dose n, n < m.

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TABLE 1. Probabilities of opiate abuse

Also, because urine samples are not collected after each dose, not all Pij are

estimable. For example, in the ARC 090 trial, urine samples were collected

only after the Sunday, Tuesday, and Thursday doses, that is, on Mondays,

Wednesdays, and Fridays. Thus, the number of doses of replacement opiate

administered between consecutive urine samples varied from 1 to 2.

Furthermore, because different addicts enter trials on different days of the

week, the number of doses of replacement opiate administered between urine

samples n and n + 1 varies from addict to addict.

Let P'kj (k = 0, 1, . . ., n) (table 1) be the probabilities of an addict using the

abused opiate before entering the trial (k = 0) and after the last administered

dose before urine sample k (k > 0) is scheduled to be collected for the treatment

group receiving the replacement opiate j. Again, not all data points are

available because of addicts missing one or more of the scheduled doses

before the urine sample k is scheduled to be collected or because of not

providing one or more scheduled urine samples, for example, for nonvisits or

because of dropping out of the study after providing u (u < k) urine samples.

The most practical way to estimate P'kj. is to assay urine sample k for the

presence of the abused opiate(s) and/or its (their) metabolites. However,

because of many reasons, more fully described in Jain’s chapter “Design of

Clinical Trials for Treatment of Opiate Dependence: What Is Missing?” (this

volume), the probability of a urine sample detecting an episode of opiate abuse

depends on several factors, primarily the duration between the last episode of

drug abuse and the time the current urine sample was obtained. Let P+kj

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(table 1) be the probability of a urine sample k for treatment j being declared

as positive for opiate. Then, in an experiment, the best that can be done is

to estimate P and hope that P+kj is the best available estimate of P' +kj kj.

There are at least three distinct possibilities for analyzing these data or

estimating P+kj. First, reduce the multiple data points for each addict to one

and then use regular inference procedures to compare the efficacy of different

treatments. For example, multiple data points obtained from urine samples for

an addict may be reduced to a single data point defined as the proportion of

positive urines, or alternatively, his or her overall profile/pattern of +/- urines can

be classified by some rank order procedure as a single rank. Let this possibility

be denoted as DATA-REDUC-1.

If sequential performance of successive units of replacement opiate is of

interest, estimates of P+kj's can be obtained, trends studied, and a summary

statistic obtained to evaluate the program performance of the different

treatments. Weights wkj can be defined in many different ways and are well

documented in statistical literature. Let this possibility be denoted as ANALSEQ-UNIT.

It will be in order here to clarify the major distinction between the summary

statistic obtained from ANAL-SEQ-UNIT and the single statistic obtained from

DATA-REDUC-1 procedures. Whereas the summary statistic obtained from

ANAL-SEQ-UNIT procedures is adjusted for differentials in treatment

performances and sample sizes over time, the single statistic obtained from

DATA-REDUC-1 basically ignores these differences in treatment performances

and sample sizes over time. However, the latter is simpler to compute and

understand.

Also, attention can be focused on only the positive urines, and a correlational

structure between time to various positive urines or failures can be studied. In

other words, data can be analyzed as a multiple failure problem. Let this

possibility be denoted as MULT-FAIL.

Some of these possibilities were explored in analyzing the ARC 090 data for

buprenorphine vs. methadone 60 mg treatment, and some of these results are

presented.

DATA-REDUC-1

If the multiple data points are reduced to one data point for each addict, one of

the first temptations would be to use some form of parametric or nonparametric

analysis of variance. However, censored observations are not permitted in

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analysis of variance, and then what is to be done with missing observations?

Both missing and censored observations can be considered as “negative” or

“positive,” as can some other combination of “negative” and “positive,” probably

depending on the reason for missing and censored observations. But then

there are at least as much “made-up” data as the real observed data. This is

probably not acceptable to most analysts.

If the proportion of positive urines, p+kj, is to be computed for addict v,v =

1, . . ., njin treatment jfor using parametric analysis of variance, the censored

and missing observations may be excluded from the analysis; that is, a different

denominator is used for each addict. This would violate the assumption that

each subject in a given treatment group is drawn from the same population. In

addition, since the probability p+kj of a positive urine for urine sample k varies

with k, the single variable y denved from multiple data points will be the sum

of u binomial variables with parameters n = 1 and P = P+tk. Is y normally

distributed and with what parameters? However, irrespective of theoretical

objection, this possibility was explored for the ARC 090 data, and the results

are given in table 2. No significant differences were observed.

An additional problem with both parametric and nonparametric analysis of

variance is that information about the pattern of positive and negative urines or

temporal correlations is lost. Also, since the kinetics of the drugs are different,

the information about the relationship between drug effect and time is lost.

Survival methods that permit censored observations can be used with a little

more confidence. However, in addition to the problem of missing observations,

the definition of what constitutes a failure may be subjective, and depending on

the definition used, the power of statistical procedure may become too low

TABLE 2. Parametric analysis of variance results for the ARC 090 study

(maintenance period only)

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(because of too few failures) or the trial may be over too soon, thus making

most of the data observed unused. For example, if the first positive urine is

used as a measure of treatment failure, ARC 090 would probably be over in a

week or so. For ARC 090, two consecutive Monday positive urines were used,

starting with the fourth Monday of treatment as the measure of treatment failure;

the results are given in table 3. No significant differences were found. KaplanMeier survival curves are displayed in figure 1. The number of failures in each

group was 25.

Another measure of treatment failure, that is, the beginning of first drug-free

period of 28 days or more, was also used. The number of failures using this

criterion was 13 in the buprenorphine group and 7 in the methadone 60 mg

group. The results are given in table 4, and Kaplan-Meier curves are plotted

in figure 2. As can be seen from table 4, the two statistics can give different

results. Only the Breslow statistics provide significant results. Hence,

depending on the definition of a failure, different methods of inference can

give different results.

Another possibility is being explored by Dr. John Harter, director of the Pilot

Drug Evaluation Division of the Food and Drug Administration, in analyzing

analgesic trials that use a combination of a sorting routine and a nonparametric

rank sum test. The sorting routine first sorts all subjects by their pain intensities

at time (sample) 1; then each distinct subgroup obtained after first sort is sorted

by its pain intensity at time (sample) 2, and so on. After the last sort, the

subjects are ranked according to their profiles in ascending or descending

order. Then, ranks are summed for each treatment group, and a rank sum test

to evaluate treatment differences may be used. This approach may also be

tried for drug abuse trials.

TABLE 3. Results of survival analysis of the ARC 090 study (maintenance

period only) using two consecutive Monday positive urines starting

with the fourth Monday of treatment as treatment failure

95-Percent Brookmeyer-Crowley

Confidence Intervals in Days

for Median Survival Time for

Buprenorphine Methadone 60 mg

Mantel-Cox Likelihood Ratio

Chi-Sq (p) Chi-Sq (p)

48.0-90.0 35.0-77.0 0.50 (.48) .09 (.77)

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FIGURE 1. Kaplan-Meier survival curves for ARC 090 study

B = buprenorphine, H = methadone 60 mg

Consider six addicts on two different treatments who have their urine results

on three samples as shown in table 5a. The subjects are first sorted according

to their results on sample 1 as shown in table 5b. Subjects 1, 3, 5, and 6 have

positive urines and as such are subgrouped first, followed by subjects 2 and

4, each of whom has a negative urine. If there were to be more than two

distinct scores, the procedure would be the same. After the first sort, the

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TABLE 4. Results of survival analysis of the ARC 090 study (maintenance

period only) using the beginning of the first drug-free period of 28

days or more as a treatment failure

Mantel-Cox Chi-Sq (p) Breslow Chi-Sq (p) Likelihood Ratio Chi-Sq (p)

2.95 (.09) 5.51 (02) 2.94 (.09)

FIGURE 2. Kaplan-Meier curves for ARC 090 study when treatment “failure”

is defined as the first drug-free period of 28 days or more

distinct subgroup of subjects 1, 3, 5, and 6 is sorted first by their results on

urine sample 2, and then the second distinct subgroup of subjects 2 and 4 is

sorted by their results on urine sample 2. This creates three distinct subgroups:

subjects 3 and 6 with a (+,+) profile; subjects 1 and 5 with a (+,-) profile; and

subjects 2 and 4 with a (-,+) profile (see table 5c). As shown in table 5d, each

of these three subgroups is then sorted by results on the third urine sample,

thus creating six distinct subgroups of subjects: subject 6 with a profile (+,+,+)

ranked 1, subject 3 with a profile (+,+,-) ranked 2, subject 5 with a profile (+,-,+)

ranked 3, subject 1 with a profile (+,-,-) ranked 4, subject 2 with a profile (-,+,+)

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TABLE 5a. Results of three urine samples from a hypothetical trial

Results of Urine Sample

Patient Identification Treatment Received

1 A

2 A

3 A

4 B

5 B

6 B

TABLE 5b. Results from a hypothetical trial after first sort

Patient Identification Treatment Received Results After First Sort

1 A +

3 A +

5 B +

6 B +

2 A

4 B

TABLE 5c. Results from a hypothetical trial after first two sorts

Patient Identification Treatment Received

Results After First

Two Sorts

3 A

6 B

1 A

5 A

2 A

4 B

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TABLE 5d. Results from a hypothetical trial after three sorts

Patient Identification Treatment Received Results After Three Sorts Rank

6 B 1

3 A 2

5 B 3

1 A 4

2 A 5

4 B 6

ranked 5, and subject 4 with a profile (-,+,-) ranked 6. For subjects with the

same profiles, average ranks can be calculated. The sum of ranks for treatment

A = 11 may then be compared with sum of ranks for treatment B = 10.

There are two problems with this approach. First, as with any nonparametric

rank test, the magnitude of treatment differences on original measurement

scale is not available. Second, this approach puts too much weight on the first

observation. For example, subject 3 with a profile of (+,+,-) is given the rank

of 2, whereas subject 2 with a profile of (-,+,+) is given the rank of 5. Both

the subjects have two out of three positives, but they are considered (almost)

opposite extremes in this approach. However, it may be possible to come

up with certain variations of this approach that do not rely on the first

observations so heavily. For example, if clinically acceptable, the first few

results may be ignored or a ranking mechanism may be developed based

on some combination of result profiles and number of positives.

ANAL-SEQ-UNIT

The first approach to explore this possibility would be to construct 2x2 tables

for each urine testing opportunity and compute, for example, a Mantel-Haenszel

z-statistic (Mantel and Haenszel 1959; Miller 1981). For the ARC 090 study,

the z-scores are displayed in figures 3, 4, and 5 when missing values are

considered as missing, negative, and positive, respectively. A consistent

pattern of superiority of buprenorphine over methadone 60 mg is observed,

except probably during the middle of the study period. However, the degree

of superiority of buprenorphine seems to be decreasing over the first half of

the study period and then increasing again during the second half of the study

period. Some, but not all, of this is explainable based on the process of selfselection as the study progresses and because of different sample sizes at

different times during the study period. The differences probably lie in different

kinetics of buprenorphine and methadone. Methadone is probably catching

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FIGURE 3. Mantel-Haenszel z-statistic for each urine testing opportunity

when missing values are considered as missing

up with buprenorphine during the first half of the study period, as may be

suggested from percent of positive urines at different times during the study,

as seen from figure 6.

However, a summary Mantel-Haenszel statistic cannot be validly calculated

from individual 2x2 tables because this summary statistic does not account

for correlations between individual 2x2 tables. How then can one calculate a

summary index of program effectiveness? First, a simple though somewhat

questionable alternative may be to score the direction of the relative efficacy of

the two drugs for each time point or urine testing opportunity and use a binomial

test to evaluate if, “overall,” one drug is more effective than the other. Another

alternative may be to use a weighted summary statistic for correlated tables as

described in Wei and Johnson (1985). However, the use of, for example, a

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FIGURE 4. Mantel-Haenszel z-statistic for each urine testing opportunity

when missing values are considered as negative

51-dimensional variance-covariance matrix as in the ARC 090 study with the

data as sparse as they are, particularly during the last few weeks of the study,

would certainly lead to some problems. For example, to solve such a huge and

sparse matrix will be numerically difficult, and the dimension of the problem will

adversely affect the power of the statistic.

The use of parametric repeated measure of analysis is even more problematic.

In addition to the inadmissibility of missing and censored observations, the

degree of robustness of repeated measure analysis of variance to analyze

binary data is unknown when there are as many repeated measures as in

these studies. Also, these studies do not generate traditional repeated

measures data. Each of the two consecutive repeated measures is interrupted

by the administration of the replacement opiate and possibly the use of opiate

of abuse. This is different when compared with using a new instructional

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FIGURE 5. Mantel-Haenszel z-statistic for each urine testing opportunity

when missing values are considered as positive

method for several months and comparing the effects of the traditional and the

new method over a period of time. It is not certain if the repeated measure

theory is applicable to these data. At best, these data seem to be multiply

interrupted time series data.

MULT-FAIL

Several authors have considered the problem of analyzing multiple failures

under various configurations (e.g., failures of the same type over time or failures

of different types at a fixed point in time and space). Recent work in this area

has been done by several researchers (Lagakos et al. 1978; Hsieh et al. 1983;

Prentice et al. 1981; Gail et al. 1980; Lawless 1987; Wei and Lachin 1984; Thall

and Lachin 1988; Wei and Stram 1988; Wei et al. 1989; Lin 1990). Some of

these authors, for example, Wei and Stram (1988) and Wei and colleagues

(1989). used a regression-based approach, whereas others, such as Wei and

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FIGURE 6. Percentpositive urines for ARC 090 study

Lachin (1984) and Thall and Lachin (1988), used multivariate versions of log

rank (Mantel 1966) and/or the Gehan test (Gehan 1965) to analyze multiple

failures. The regression approach of Wei and colleagues (1989), which is a

multivariate version of Cox’s proportional hazards model (Cox 1972), imposes

the least restrictive structure on recurring events (failures) and thus is very

appealing.

The regression approach of Wei and colleagues (1989) will be an excellent

choice if the number of failures in the model is limited and there are many

subjects in the study. In the ARC 090 study, the number of subjects, 162

across three treatment groups, was probably sufficient to use this model,

but each subject could also experience up to 51 failures in the 17-week

maintenance phase of the study. Hence, to use this model, there was no

choice but to use an algorithm that reduces the maximum number of failures

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to 17. Even though this approach does permit censored observations, the

missing observations must still be handled in some way. In fact, the algorithm

used to reduce 51-dimensional data to 17-dimensional data more or less solved

this problem, except when all three samples during a week were missing.

A weekly index was developed for urine samples being positive or negative for

opiates. If at least one of the three samples was positive or all samples for a

given week were missing, that week was considered to be positive for opiates.

Otherwise, that week was considered to be negative for opiates. Thus, the

maximum number of failures was limited to 17 for this analysis. However, to

avoid too many ties, the time (in days) to each failure used to compute various

statistics was defined as the time to first positive urine or missing observation (if

all observations were missing during a week) during the week in consideration.

This algorithm does result in some loss of information, for example, one who

has three positive urines during a week is treated the same way as one who

has only one positive urine during that week. Hopefully, this loss of information

will be random and uniform across different treatment groups and will result in a

valid comparison. No formal statistical tests were done to verify this.

Only one covariate-that is, treatment assignment-was used for analyzing

ARC 090 data (1 = buprenorphine, 0 = methadone 60 mg). Thus, 17 regression

coefficients, one for each week, were estimable. A joint test of hypothesis

testing Hk:ßk = 0, k = 1, . . ., 17 was conducted. An estimate of common

regression coefficient, 17 was also obtained and tested

for = 0. The weights cj were optimally calculated by the program MULCOX

(Lin 1990). A negative regression coefficient indicates a decreased hazard

rate for buprenorphine compared with methadone 60 mg, that is, a negative

regression coefficient favors buprenorphine treatment. Also, a hazard ratio

of less than one favors buprenorphine treatment. The hypothesis Hk:ßk = 0

was not rejected (Wald statistic with 17 degrees of freedom = 20.89, = .23).

However, the estimate of cjßj was found to be significantly different than

zero ( = -0.294, p = .04), indicating an “average” superiority of buprenorphine

over methadone 60 mg. The 95-percent confidence interval for the common

hazard ratio of .746 was (.566, .983).

The hazard ratios for each week are plotted in figure 7 indicatlng consistent

superiority of buprenorphine.

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FIGURE 7. Hazard ratios for each week for ARC 090 study

WHAT ARE THE PROBLEMS?

The biggest problems in analyzing these data are:

1. The order of dimension (51-dimensional)

2. The sparseness of data

3. The problem of missing values

None of these problems seems to be handled too well by any of the possibilities

explored in this chapter. DATA-REDUC-1 methods do reduce the data to

one dimension but at a tremendous cost-complete loss of information about

correlational structures between various dimensions and more or less no

ability to handle missing and/or censored observations. In fact, some of the

DATA-REDUC-1 methods make no distinction between missing and censored

observations. ANAL-SEQ-UNIT methods do handle one dimension at a time

but have difficulty combining information unless some sort of miniature data

reduction scheme can be implemented. MULT-FAIL methods do handle

censored data, but heavy censoring causes loss of power, and dimension

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of data must be reduced somewhat by using a miniature data reduction

scheme. However, the possibly informative nature of censoring causes

interpretational difficulties. The sparseness is either ignored or subjectively

handled in DATA-REDUC-1 and ANAL-SEQ-UNIT methods.

None of the methods has any ability to handle missing values without outside

intervention. The solution may be to consider a missing observation as the

third stage as discussed by Weng (this volume). Another possibility suggested

by Dr. Gross of the Medical University of South Carolina is to consider a

quadrinomial model with four categories—positive, negative, missing, and

censored-and then to consider a conditional binomial model in which

conditioning is on the later two categories.

OTHER PRIMARY VARIABLES AND THEIR ANALYSES

One of the other three primary variables of interest in these clinical trials is the

retention rates in the treatment program. These data can easily be analyzed

by any one of the survival analytic techniques. However, the problem of

informative dropouts may have to be handled in some way. Some of the work

in this area is due to Dr. Margaret Wu of the National Heart, Lung, and Blood

Institute (Wu and Bailey 1988, 1989; Wu and Carroll 1988).

One of the self-reported measures of drug abuse is the “craving” scores

obtained periodically during the course of the study. Before entry into the trial

(time 0) and at times i, i = 1, . . . , m, addicts are asked to report how much

craving or need or desire they had during the last few days (e.g., a week or

since the last time they visited the clinic) for the abused drug. Usually they are

asked to “mark” the intensity of their craving or need on a 100-mm-long line

called a craving scale, such as the one shown in figure 8. A score of zero

means no craving, and a score of 100 means the most intense craving ever

experienced. Let Sij, be the craving scores reported by an addict on treatment

j at time i, i = 0, 1, . . ., m. These data, like the urine data, have missing and

censored observations. There are several ways to analyze these data.

Regression analysis can be performed on either Sij (i = 0, . . ., m) or on Sii -

S0j (i = 1, . . ., m), and standard tests for ß = 0 or ßj-ßk, = 0 can be performed.

Alternatively, regression analysis for multiple failures based on proportional

hazards model such as those described by Wei and colleagues (1989) can

also be used.

Another important outcome variable in the drug abuse trials IS the physician’s

(or staff’s or patient’s) global impression of an addict’s status with respect to

his or her drug-seeking behavior at different time points during the study as

compared with a previous time point or compared with his or her status at the

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FIGURE 8. Craving scale used in drug abuse research

time of entry into the study. Generally, these physician’s (or staff’s or patient’s)

scores are obtained on a 3- to 5-point rating scale. These data can be

analyzed the same way as craving scores data, or in addition, change in the

status can be evaluated by a one-sample or two-sample (Feuer and Kessler

1989) McNemar’s chi-square test statistic.

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ACKNOWLEDGMENT

An earlier version of this chapter was reviewed by Dr. Alan J. Gross of the

Medical University of South Carolina; his helpful comments led to certain useful

changes in this version of the chapter.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

134
Summary of Discussion: “Analysis

of Clinical Trials for Treatment of

Opiate Dependence: What Are the

Possibilities?”

Ram B. Jain

During my talk I made a comment about the difficulty of explaining certain

statistical methods to clinicians. Dr. Gorodetzky thought the likelihood of

explaining the details of some of the statistical analysis to clinicians is very

remote. If the statisticians can agree on what is an appropriate method of

analysis, a qualitative discussion or description of the method along with

discussion of results in relation to analysis would be sufficient. For Dr. Fisher,

war was too important to be left to generals. He would not hesitate to speak

on clinical matters, and sometimes the best statistical ideas do come from the

clinicians. Dr. Gorodetzky remarked,

I think the real problem is sometimes we tend not to talk

each other’s languages, and we tend to be way out here

clinically and way out here statistically. If we can come

a little bit more towards the middle with a little bit of

mathematical understanding from a clinician and a little

bit of clinical understanding from the statistician, there

can be a very productive interchange.

Dr. Geller found pictures (e.g., cumulative hazard plots) to be very useful in

helping clinicians understand some complicated statistical concepts. One

should not try to explain every little detail because it is really not important to

clinicians.

Dr. Geller found ranking methods to be a rich tool for analyzing multiple

endpoints data (e.g., proportion positive and proportion missing) also.

However, there may be some price to pay (e.g., loss in power) when

parametric methods are applicable but nonparametric procedures are

used. In addition, magnitude of treatment effects is not easily discernible

when ranking methods are used. There are ways to go back to the original

135
unranked data, but they do not always work and may not always be desirable.

Dr. Fisher did not think one should necessarily be tied to description of, for

example, magnitude of treatment effect going along precisely with the specific

test of hypothesis used to compute values.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

136
Toward a Dynamic Analysis of

Disease-State Transition Monitored

by Serial Clinical Laboratory Tests*

T.S. Weng

INTRODUCTION

In many clinical trials dealing with the monitoring and/or management of

a chronic disease under medical treatment, it is customary to follow each

patient up to some censoring time. The observations usually consist of

longitudinal counts of patients in cohorts with common disease states

identified by an ad hoc laboratory test repeatedly administered over a fixed

sequence of time points. For example (see Jain’s chapter, “Analysis of Clinical

Trials for Treatment of Opiate Dependence: What Are the Possibilities?,” this

volume), in a randomized clinical trial (ARC 090) to evaluate the efficacy of

buprenorphine for the treatment of opiate addiction, 162 qualified patients were

put through a 17-week maintenance phase in three separate treatment groups:

Group 1 was maintained on 8 mg of buprenorphine administered sublingually

daily, and groups 2 and 3 were maintained on 20 mg and 60 mg, respectively,

of methadone (positive control) administered orally daily. To evaluate the

frequency of opiate abuse, all patients were asked to provide urine samples

three times weekly on Mondays, Wednesdays, and Fridays. These samples

were assayed to detect the presence of opiates (mainly heroin or morphine).

A positive sample was defined as a possible treatment failure. Due to missed

clinic visits or other reasons, 19.8, 17.7, and 17.7 percent, respectively, of urine

samples from the three treatment groups were uncollected. Furthermore, the

percentages of patients lost to followup in these groups were noted to run up

to 60.4, 80.0, and 63.0 percent, respectively. If it were not for the massive,

possibly nonrandom missing observations and loss of patients to followup,

as well as for the seemingly time-dependent nature of the data encountered,

this clinical trial could have been analyzed by the popular method of survival

analysis using either the multivariate versions of Gehan’s log-rank tests (Gehan

1965; Peto and Peto 1972; Wei and Lachin 1984) or the generalized versions

*The views presented here are those of the author. No support or endorsement by the Food and

Drug Administration is intended or should be inferred.

137
of Cox’s semiparametric, proportional hazard model for censored failure time

with covariates acting as treatment responses (Prentice et al. 1981; Gail 1981;

Wei et al. 1989; Lin 1990).

The purpose of this chapter is to propose a stochastic compartmental model

as an alternative for modeling the data generated from the aforementioned

study, thereby evaluating the efficacy of buprenorphine against methadone in

the treatment of opiate addiction. The plan of this chapter is as follows: First,

a closed three-compartment system is introduced by which patients are

classified according to their patterns and directions of response to medication

during the course of treatment. This is followed by the introduction of a Markov

process, which provides a natural context for addressing the problem of

statistical dependence among successive observations and characterizes the

dynamics of disease-state transition within the compartmental system. Based

on the assumption that this synthesized stochastic compartmental model is

piecewise stationary in time, an iterative weighted conditional nonlinear leastsquares procedure is then developed to facilitate parameter estimation. The

results are then applied to analyze the ARC 090 study to draw conclusions on

the efficacy of buprenorphine treatment. Finally, a general discussion is given.

COMPARTMENTAL MODEL

The patient pool in the ARC 090 study can be partitioned into three cohorts

or compartments (see figure 1 below) that are each numbered 1, 2, or 3

depending on whether they encompass patients who have tested negative (-)

for opiates, positive (+) for opiates, or have missed the test with the potential

for being lost to followup (M/L). In figure 1, the compartments are represented

as boxes with arrows between boxes indicating the direction of disease-state

transitions, Let N be the total number of patients and N,(t) be the number of

patients in compartment i (i = 1,2,3) at time t > 0 and let denote the

transition rate from compartment i to compartment j (i,j = 1,2,3) at time t > 0.

Patients will then be included in different compartments depending on the

results of their urinary tests or on whether they comply with the urinary test

schedule. This compartmental system, within which all compartments (or

states) communicate with one another, is regarded as closed in the sense

that jNj(t) = N at any time t > 0. The individual patients in the system are

assumed to act independently without being influenced by others.

STOCHASTIC PROCESS

The dynamics of changes in disease states within this system may be described

by a Markov process {X(t): 0 < t < } defined on the state space S = {1,

negative; 2, positive; 3, missing or lost to followup} with the associated transition

138
FIGURE 1. Schematic diagram of a closed three-compartment model

with representing rates of transition between pairs of

compartments at time t > 0 (i,j = 1,2,3)

probability matrix (or transition matrix, for brevity) P(t,t0) = [Pji(t,t0)], 0

and the transition rate matrix (or rate matrix, for brevity) K(t) =

where

Pji(t, t0 = Pr {X(t) = j|X(t0) = i}, (3.1)

(3.2)

For the time being, let for all i,j so that (X(t)} becomes a stationary

process with P(t,t,) being a function of t - t0, only. Without loss of generality,

therefore, it may be assumed that t0 = 0, so one can simply write P (t) = P(t,0)

Under these assumptions, the transition matrix P(t) is uniquely given by the

Kolmogorov forward differential equation

(3.3)

with the initial condition P(0) = I, a 3x3 identity matrix. In the above equation,

the rate matrix K is singular, as can be seen by the expressions in (3.2). Thus,

the eigenvalues of K are given by 0, ,and -ß (0 < a, ß < 1; ß where

139
with

The explicit forms of the elements of P(t) = [Pji(t)] are then given by (Chiang

1980, pp. 416-426):

(3.5)

140
It is noted that

(3.6)

and that for all i,

(3.7)

The known as the (asymptotic) state probabilities, are independent of the

initial state i. It is further noted that the elements of the rate matrix K contain

structural information about the process, for example,

expected length of time (or mean residence time) for

a patient in state i to remain in that state. (3.8)

Also useful for checking the validity of parameter estimates (see section titled

“Analysis of the ARC 090 Study and Conclusion”) are the relations

(3.9)

and

(3.10)

which follow immediately from expression 3.4.

WEIGHTED CONDITIONAL NONLINEAR LEAST-SQUARES ESTIMATION

Suppose that the Markov process {X(t)} is piecewise stationary (Faddy 1976)

so that the transition rates K(t) = may take on different sets of constant

values for disjoint segments (time Intervals) of {X(t)}. These stationary

segments are in fact chosen to approximate the true process, which may be

time dependent. The chosen segments should each contain a sufficient

141
number of observations to make the parameters (namely, the transition rates)

statistically estimable. To fix the idea, let

(4.1)

so that for each time interval a unique solution P(t - ) to equation

3.3 can be obtained in the same fashion that led to the explicit form given by

equation 3.5. Suppose that within each such interval, observations are made

at times t0 Let there be Nj

(h-1) patients in state i

(i = 1,2,3) at the end of the preceding segment, and for the sake of notational

convenience, this number will be used interchangeably with Ni

(h)(t0

). For now,

let h be suppressed so that it will not be used to index the related expressions

in the subsequent discussion. Furthermore, let uk = tk - tk-1 k = 1,...,m, and

suppose that the data consist of the number Xji(uk) of patients who occupy state

i at time tk-1 and state j at time tk, i = 1,2,3, j = 1,2,3, k = 1,...m, where, by abuse

of notation, the total number m of observations in a particular segment may not

be the same as in the other. Then, given Nj(tk-1) for i = 1,2,3, the component

variables in each of the vectors

X j( u k) = [x 1 i ( u k) x 2 i ( u k) x 3 i ( u k) ] (4.2)

where means transposition, will follow a trinomial distribution with parameters

Nj(tk-1), P1i(uk), P2i(uk) and P3i(uk) = 1 - P1i(uk) - P2i(uk). Let us also write

(4.3)

and

For simplicity, let us drop the argument uk momentarily. It IS thus easily seen

that, for each i (i = 1,2,3),

142
At this point, it should be noted that the goal for this section is to set up a

statistical model to estimate the parameters in each of the stationary pieces (or

segments) of the Markov process {X(t)} represented by the parameter vector

which will sometimes be written in an alternative expression as

(4.5a)

Because in the above equation the variance-covariance matrix of Yi is

singular with rank equal to 2, we may proceed to estimate by utilizing just the

2x2 principal minor along with the 2-vectors Pi* and Yi* obtained by

deleting the third elements of (4.3) and (4.4), respectively (i = 1,2,3). Next, let

us string together these two sets of 2-vectors separately to form the following 6-

vectors:

Q = [P1*', P2*', P3*']'

and

a Z = [Y1*', Y2*', Y3*']'. 

It then becomes obvious that

E(Z) = Q

and

Var(Z) = Diag[ say.

By replacing the argument uk, we can now write a statistical model as follows:

Z(u,) = Q(uk) + e(uk), k = 1,...,m, (4.6)

where the elements of Q(uk) are nonlinear functions of E{e(uk)} = 0, and

Var{e(u,)} = (uk) for all k. It remains to find the least-squares estimates for the

parameters by fitting the data from the ARC 090 study, prearranged in the

143
form (4.4), to the nonlinear model (4.6). Before taking this step, let us make a

linear transformation of model (4.6) to remove the statistical dependence in its

error structure. Note that each of the diagonal blocks (uk) in (uk) has the

following expression:

where the argument uk is again suppressed. Because the variance-covariance

matrix (uk) is positive definite, there exists a nonsingular lower triangular

matrix T(uk) such that

Specifically, T(uk) = Diag[T1(uk), T2(uk), T3(uk)] with

the argument uk having been omitted. By virtue of the matrix T(uk), we can then

deal with the new transformed model

T

1

(uk)Z(uk) = T

1

(u k)Q(uk) + e(uk), k = 1,...,m, (4.7)

where = T

-1

(uk)e(uk

) is the new error term with

a 6x6 identity matrix. Thus, we see that the new model (4.7) has achieved an

independent error structure. Based on this model, we can now find the leastsquares estimate for by minimizing the object function

(4.8)

144
This may be achieved by an iterative SAS function minimization program (SAS

Institute, Inc. 1988, chapter 23) using the derivative-free DUD option (Ralston

and Jennrich 1978). The starting values for can be derived from the

maximum likelihood estimates (MLEs) for the transition probabilities Pji

associated with a discrete-time Markov chain {X(k): k = 1,2,...} resulting from

the original continuous-time Markov process {X(t): 0<t< } when periodic

observations are made on the latter. Specifically, let Xji(k) be the number of

transitions i j during the interval uk = tk- tk-1, k = 1,2,...m, where m is the total

number of observations made within a particular stationary segment of {X(t)}.

Then, given the initial state i (i=1,2,3), the joint trinomial distribution of Xji(k),

aggregated over k, will produce the MLEs of Pji in the form

(4.9)

where Ni(k - 1) = is the number of patients in state i at time tk-1, k =

1,2,...,m. If we denote by u the length of the interval between successive

observation times, then it follows from the first equation of (3.2) that

Pji/u, j j (4.10)

Because, according to the study design, observations were taken every other

day except for the weekend, we can roughly set u = 2 and use the quotient

= Pji/2 as the initial estimate for (i,j = 1,2,3). These values are in turn

substituted in equation (3.4) to obtain the initial estimates for a and ß.

ANALYSIS OF THE ARC 090 STUDY AND CONCLUSION

Some details on this clinical trial have been given in the introduction. For the

purpose of saving space, only a subset of the observed data is presented here

(table 1). The first column gives the treatment indicator TRT, which has value 1

if the treatment was buprenorphine, 2 if it was methadone 20 mg, and 3 if it was

methadone 60 mg. The second and third columns give, respectively, the serial

observation times t (three times per week taken on Monday, Wednesday, and

Friday) and the intervals u in days between successive observation times.

These are followed by three columns of state totals Ni (i = 1,2,3) representing

the total numbers of patients in state i at various observation times. Because

the state total N3 is of composite nature, it is further split into two components,

M and L, which occupy the next two columns, with M and L representing,

respectively, the number of patients who missed the urinary test and the

number of patients who were lost to followup. The last nine columns are

145
TABLE 1.

Transition Count

TRT

SUM

MLE

2

2

2

2

2

2

2

2

2

2

SUM

MLE

t

0

1

2

3

4

5

6

7

8

9

10

11

12

0

1

2

3

4

5

6

7

8

9

0

1

2

3

Partial listing of observed data from ARC 090 study

Stale Total N 3

x 3 1

0

1

2

3

1

0

2

1

1

2

1

4

18

.07

0

3

1

2

2

1

9

0

0

18

.15

0

3

3

U

0

2

2

3

2

2

3

2

2

3

2

2

3

0

2

2

3

2

2

3

2

2

3

0

2

2

3

N1 N 2

(M, L)

7 36

17 30

27 18

23 19

22 18

26 13

26 16

21 16

23 13

28 12

25 12

26 10

N 3

10

6

8

11

13

12

11

16

17

13

16

17

(10.0)

(5.1)

(6, 2)

(8, 3)

(7, 6)

(6, 6)

(5, 6)

(7, 9)

(7, 10)

(3, 10)

(5, 11)

(6, 11)

294 189 153

2 46 7 (7, 0)

18 29 8 (8, 0)

16 31 8 (8, 0)

17 28 10 (8, 2)

15 25 15 (11, 4)

15 21 19 (14, 5)

19 20 16 (8, 8)

6 25 24 (14, 10)

10 25 20 (8, 12)

118 250 127

6 43 5 (5, 0)

16 32 6 (6, 0)

22 23 9 (7, 2)

17 23 14 (10, 4)

X1 1 x 2 1

5 2

14 2

20 5

17 3

21 0

24 4

20 4

18 2

20 2

23 3

22 2

20 2

224 31

.82 .11

2

10

14

12

8

9

3

3

7

68

.58

5

11

15

0

5

1

3

5

5

7

3

3

32

.27

2

2

4

x 1 2 x 2 2 x 3 2

7 24 5

11 14 5

3 11 4

3 14 2

4 10 4

2 9 2

1 10 5

5 7 4

6 7 0

2 8 2

2 7 3

4 6 0

50 127 36

.24 .60 .17

15 23 8

5 23 1

2 24 5

1 2 1 6

5 16 4

6 13 2

2 13 5

4 18 3

5 15 5

45 166 39

.18 .66 16

10 28 5

9 19 4

1 16 6

x 1 3

5

2

0

2

3

0

0

0

2

0

2

1

17

.11

1

1

1

2

2

4

1

3

2

17

.13

1

2

1

x 2 3 x 3 3

4 1

2 2

3 5

1 8

3 7

3 9

2 9

4 12

3 12

1 12

1 13

2 14

29 104

.19 .69

6

3

3

1

0

2

5

4

1

25

.20

3

2

3

0

4

4

7

13

13

10

17

17

85

.67

1

2

5
TABLE 1.

TRT

t

333333

SUM

MLE1111111111111111

SUM

MLE

36

37

38

39

40

41

42

43

44

45

46

47

46

49

50

51

2 42 2 43 2 44 2 45

(continued)

State Total

U

N

1

N

2

N

3

2232233223223223223223322316 23 15 (11, 4)

18 20 16 (11, 5)

14 22 18 (7, 11)

18 20 16 (3, 13)

16 21 17 (4, 13)

143 227 116

14

6

4 (4.29)

15

4

5 (5, 29)

1374 (4, 29)

13

56 (5, 30)

1275 (4, 30)

1626 (5, 30)

1338 (7, 30)

14

55 (4, 30)

1563 (2, 30)

13

47 (6, 30)

147

3 (2, 30)

1473 (2, 30)

1428 (7, 30)

1167 (6, 30)

147

3 (1, 31)

205375578

(1, 43)

(1, 43)

(1, 43)

(0, 44) N 3

(M, L)

x 1 1x 2 1x 3 1x 1 2x 2 2x 3 2x 1 3x 2 3x 3 3

9625 14

10

337 13

11522 13

1022

7 14

13502 16

11

32

4 14

95 3 1 17 47 147

.66 .22 .12 .21 .65

3

9

4 10 4 11 4 13 0 15 2 13

25 79

.22 .68

130

11

11311

922

4

8502

11

0

14

10 1 50

10 1 22

103

1

2

10323

11

20

1

11213

11033

9321

10

1

0

3

11 1 23

155 27 23 33

.76 .13 .11 .42

1

2

22

13

13

0

4

03

33

02

03

23 1 2 1 2 3 4 3 3 0 3

18 42

.23 .55

333041001321

322122131341032

30

.39425

435123

33

.15211210002003102

15

.19100

211112

12

.10110213230200110

17

.22101

000010
TABLE 1.

TAT t

2 46

2 47

2 46

2 49

2 50

2 5 1

MLE

42

43

44

45

46

47

48

49

50

5 1

u N1 N 2

2 4 6

2 3 8

3 4 7

2 3 7

2 4 7

3

38 59

3 11 10

2 11 10

2 13 7

3 9 4

2 7 6

2 7 6

3 7 8

2 5 10

2 7 5

3

77 70

(continued)

State Total N 3

N 3

(M, L)

2 (1, 44)

1 (0, 44)

1 (0, 44)

2 (1, 44)

1 (0, 44)

11

4 (4, 29)

4 (3, 30)

5 (2, 32)

12 (8, 33)

10 (6, 33)

10 (6, 33)

10 (6, 33)

10 (5, 34)

13 (7.35)

78

x 1 1 x 2 1

4 0

3 1

2 1

3 1

3 0

3 1

27 9

.71 .24

9 1

9 1

8 0

6 1

5 1

3 4

2 4

5 0

6 1

51 15

MLE .66 .20

KEY: M = missing; L = lost; TRT = treatment; SUM = sum; MLE = maximum likelihood estimate

x 3 1

1

0

0

0

0

0

2

.05

1

1

5

2

1

0

1

0

0

11

.14

Transition Count

x 1 2

0

0

2

0

1

0

9

.15

X2 2 x 3 2 x 1 3

6

6

6

6

6

6

47

.79

2 6

3 6

1 4

0 4

2 5

3 4

2 5

2 4

2 3

17 43

.24 .61

0

0

0

1

0

1

3

.05

0

1

2

0

1

1

1

4

0

10

.14

0

0

0

0

0

0

2

.18

0

1

0

1

0

1

1

0

0

4

.05

X 2 3

0

1

0

0

1

0

2

.18

1

0

0

3

2

0

1

1

2

10

.13

x 3 3

1

1

1

1

1

1

7

.64

3

3

5

8

8

9

8

9

11

64

.82
allocated to the transition counts Xji (i,j = 1,2,3) representing the number of

patients who were observed to undergo the transition i j during an interval u.

At the bottom of each segment the sums of Ni and Xji are given, followed by the

MLEs for transition probabilities calculated from equation (4.9).

To estimate the parameters in (4.5), the observed serial data were partitioned

into disjoint stationary segments (3 to 6 weeks in length), which were empirically

identified and fitted to the model (3.5). These segments were selected by trial

and error to ensure the following: (1) a convergence for the weighted

conditional nonlinear least-squares estimation procedure described in the last

section-the convergence criterion used was “S < 10-8”; (2) a reasonable

closeness between the estimate of and that of

see equation (3.9); and (3) a good fit of the data to the model. The data

from treatments 1, 2, and 3 comprised four, five, and four such segments,

respectively. Of these, the first and the last segments from each treatment are

shown in table 1. It should be noted that, barring the first segment for each

treatment, all subsequent segments contained data from only those patients

who had stayed in the study long enough to enter into these segments,

although some of the segment members might still fail to stay for the whole

segment-for example, taking the last segment of treatment 1, the 29

(cumulative) losses at the end of the preceding segment were not counted,

whereas the two losses (= 31 - 29) that occurred during this last segment

remained nominally counted. Moreover, data from the week between the fourth

and the fifth segments for treatment 2 as well as those from the week between

the second and the third segments for treatment 3 were omitted because

inclusion of them in either of the neighboring segments would have resulted in

poor fit of the data to the model. Table 2 lists by treatment and segment the

least-squares estimates of the transition rates and the transition

probabilities [Pji(u)], where u = 2 days if transition counts were made every other

day during weekdays and u = 3 days if counts were made over weekends.

As can be seen from the last block of columns in table 2, the observed data,

after having been partitioned into empirically identified stationary segments,

appear to accord well with the model. With estimates for the rate matrix and the

transition matrix in place, some useful information may now be extracted from

these estimates. Here the transition rates measure on a daily basis the

propensity for a patient to move between pairs of disease states, granting that

149
TABLE 2. Least-squares estimates of transition rates and transition probabilities for empirically identified stationary

segments, listed by treatment
TABLE 2. (continued)
TABLE 2. (continued)
transition does take place, and these rates are in turn related to Pji(u), u = 2 or

3, by equations (3.2) and (4.10). Now let us proceed with comparison of

treatment effects by looking into the difference over successive

segments, as given below:

Segments: 1 2 3 4 5

Buprenorphine: 0.047 0.055 0.054 0.156

Methadone 20 mg: -0.051 -0.049 -0.060 -0.054 -0.042

Methadone 60 mg: -0.005 0.015 0.044 0.024

From these comparisons it is clear that, in contrast to both buprenorphine and

methadone 60 mg, methadone 20 mg tended to induce a greater rate of

transition from state 1 to state 2 than from state 2 to state 1 (which refers to an

improvement in the clinical sense); however, buprenorphine is superior even to

methadone 60 mg because, from the first segment on, it reversed the direction

of transition in its favor, with its strength culminating in an impulsive surge at the

last segment. This tendency appeared to be unperturbed by the continual

loss of patients during the course of the study because (1) between-group

differences were seen to be highly consistent from the first segment (which had

kept all patients formally under observation) till the last segment (which left out

all patients who had been lost to followup in the preceding segments), and (2)

both the buprenorphine group and the methadone 60 mg group had about the

same patient-loss rate (63.0 percent for the latter vs. 60.4 percent for the former

according to Jain, “Analysis of Clinical Trials,” this volume) during the course of

the study. However, the substantially increased loss rate (80.0 percent) seen in

the methadone 20 mg group could mostly be ascribed to its poor performance.

The above observation is also applicable to Pji(u), which refers to the likelihood

of the transition i j (j i) during an interval u. This likelihood tended to be

greater with u = 3 days than with u = 2 days, irrespective of the direction of

transition. That is, more transitions are likely to occur during weekends than

during weekdays.

Put in another perspective, the effect of treatment may also be reflected by the

duration of improvement defined as the mean length of time a patient spends in

state 1 during each segment-see expression (3.8) and table 3. It was found

out that, once the patient had been in state 1 (i.e., negative for opiate), he or

she stayed there much longer when on buprenorphine (7.9 to 11.5 days) than

when on methadone 20 mg (4.7 to 6.9 days), with his or her duration of

improvement ranked in between when on methadone 60.mg (5.9 to 9.9 days).

The same was also true when the effect of treatment was evaluated in terms of

the asymptotic state probabilities for the successive segments-see equation

(3.7) and table 3. These state probabilities may be interpreted as the expected

state-specific proportions of patients in the population, assuming that each

153
TABLE 3. Mean residence time and asymptotic state probabilities

Mean Residence Time Asymptotic State Probability

Seg Wks St 1 St 2 St 3

1 4 11.5 5.4 7.0 .474 .266 .260

2 3 7.9 4.3 6.1 .419 .288 .293

3 5 8.8 4.6 8.6 .403 .244 .353

4 5 8.2 3.3 4.4 .566 .208 .226

1 3 4.7 6.1 6.2 .268 .414 .318

2 4 4.6 7.0 10.2 .183 .397 .420

3 3 5.3 6.0 8.8 .249 .409 .342

4 3 4.8 5.0 6.5 .264 .412 .324

5 3 6.9 9.8 5.2 .353 .527 .119

1 3 5.9 5.7 6.3 .325 .381 .294

2 4 6.6 5.4 6.3 .354 .352 .293

3 6 9.9 5.6 6.8 .465 .308 .227

4 3 5.9 5.2 11.2 .271 .285 .444

Treatment = Buprenorphine

Treatment = Methadone 20 mg

Treatment = Methadone 60 mg

segment continues to maintain its own stochastic characteristics beyond the

segmental cutoff point.

Based on the results of this section, we may draw the following conclusion:

Relative to methadone, buprenorphine, as demonstrated in a randomized

comparative clinical trial, is found to be a substantially effective drug indicated

for the treatment of opiate addiction with steadfast action-patients on

buprenorphine treatment tend to achieve an opiate-negative state faster, and

on reaching that state, they stay there longer.

DISCUSSION

The stochastic compartmental model proposed in this chapter provides a

probabilistic description of disease-state transitions for opiate-addicted patients

under medical treatment whose disease states were monitored by serially

administered urinary tests. The result of a test at each visit was retrospectively

assigned to one of three compartments numbered 1, 2, and 3 according to

154
whether it was (1) negative for opiate, (2) positive for opiate, or (3) test was

missing or patient was lost to followup. The dynamics of changes in the

disease state were then analyzed by a regular (all transition probabilities being

nonzero) three-state continuous-time Markov process with constant transition

rates. The author is aware of the fact that lumping patients who missed the

urinary test and those who were lost to followup in a composite compartment,

numbered 3 in the above, would result in underestimated rates of transition out

of that compartment. Therefore, these rates were deliberately slighted in the

reporting of results because they were not as important as the remaining ones,

which still contain unabridged information. In theory, it is known that an

arbitrary rearrangement of the state space associated with a Markov chain may

render the new chain non-Markovian (Kingman 1972; Kemeny and Snell 1960).

In applications, however, all that is required is that the model employed be

sufficiently near to reality. Therefore, rearrangements are often made on states

regarded as less germane to the question of interest (Bartholomew 1982; Fix

and Neyman 1951). The three criteria, (1) through (3), used in the preceding

section for identification of stationary segments as well as the partial truncation

of lost patients from successive segments are in fact the embodiment of

practical efforts made to ensure that the theoretically coarser model employed

in the analysis is sufficiently correct. Naturally, we could have separated the

two states M and L in compartment 3 to model the data via an absorbing

Markov chain or, perhaps, via a semi-Markov process. However, this would not

only introduce more parameters to be estimated but also shift the focus of the

problem toward examining the clinically less important parameter, namely, the

mean absorption time. The author is nevertheless still intent to pursue the

problem along these lines as a supplementary analysis of the ARC 090 study.

Originally, the ARC 090 data set did contain values of several prognostic

variables such as the age and sex of the patient. However, the possible effects

of these variables were not taken into consideration in the model employed

above. Based on the fact that the ARC 090 trial was a genuine prospective

study having been executed under strict adherence to the principle of

experimental design and randomization, it is deemed unlikely that the treatment

comparisons had been severely confounded by these covariates.

It is also perhaps proper and necessary to add that the SAS program for

function minimization utilized to estimate the rates of disease-state transition

was capable of providing neither a valid asymptotic standard error for each of

the estimates nor an asymptotic correlation matrix for them. This limitation has

precluded the present approach to the analysis of the ARC 090 study from

going into the realms of interval inferences and/or hypothesis testings. It is

hoped that this deficiency will be resolved subsequently.

155
REFERENCES

Bartholomew, D.J. Stochastic Models for Social Processes. New York: Wiley,

1982.

Chiang, C.L. An Introduction to Stochastic Processes and Their Applications.

New York: Krieger, 1980.

Faddy, M.J. A note on the general time-dependent stochastic compartmental

model. Biometrics 32:443-448, 1976.

Fix, E., and Neyman, J. A simple stochastic model of recovery, relapse, death,

and loss of patients. Hum Biol 23:205-241, 1951.

Gail, M.H. Evaluating serial cancer marker studies in patients at risk of recurrent

disease. Biometrics 37:67-78, 1981.

Gehan, E.A. A generalized two-sample Wilcoxon test for comparing arbitrarily

singly-censored samples. Biometrika 52:203-223, 1965.

Kemeny, J.G., and Snell, J.L. Finite Markov Chains. Princeton, NJ: Van

Nostrand, 1960.

Kingman, J.F.G. Regenerative Phenomena. New York: Wiley, 1972.

Lin, D.Y. MULCOX: A computer program for the Cox regression analysis of

multiple time variables. Comput Methods Programs Biomed 32:125-135,

1990.

Pete, R., and Peto, J. Asymptotically efficient rank invariant test procedure (with

discussion). J Roy Stat Society, Ser. A 135:185-206, 1972.

Prentice, R.L.; Williams, B.J.; and Peterson, A.V. On the regression analysis of

multivariate failure time data. Biometrika 68:373-379, 1981.

Ralston, M.L., and Jennrich, R.I. DUD, a derivative-free algorithm for nonlinear

least squares. Technometrics 20:7-14, 1978.

SAS Institute, Inc. SAS/STAT User’s Guide, Release 6.03 Edition. Cary, NC:

SAS Institute, Inc., 1988.

Wei, L.J., and Lachin, J.M. Two-sample asymptotically distribution-free tests for

incomplete multivariate observations. J Am Stat Assoc 79:653-661, 1984.

Wei, L.J.; Lin, D.Y.; and Weissfeld, L. Regression analysis of multivariate

incomplete failure time data by modeling marginal distributions. J Am Stat

Assoc 84:1065-1073, 1989.

ACKNOWLEDGMENT

Dr. Harry F. Bushar and Professor Joel B. Greenhouse made helpful comments

on an earlier draft of this chapter.

AUTHOR

T.S. Weng, Ph.D.

Mathematical Statistician

156
Division of Biometric Sciences, HFZ-162

Office of Science and Technology

Center for Devices and Radiological Health

Food and Drug Administration

Suite 405

1801 Rockville Pike

Rockville, MD 20852

157
Summary of Discussion: “Toward a

Dynamic Analysis of Disease-State

Transition Monitored by Serial Clinical

Laboratory Tests” by Weng*

Alan J. Gross

In his chapter, Dr. Weng considers a three-compartment model applicable

to data generated from a randomized clinical trial designed to evaluate the

efficacy of buprenorphine for the treatment of opiate addiction. The model

allows for missing observations due to schedule noncompliance or lost-tofollowup patients.

Although the transition probabilities are expected to be time dependent, the

time axis is subdivided into intervals over which the transition rates are

assumed to be constant.

As indicated during the discussion, several generalizations of this model are

possible:

A four-compartment model can be considered whereby those patients

who are lost to followup or censored are in a compartment separate from

the noncompliant patients. Since such patients always remain in this

compartment once they have entered it, it is an absorbing compartment

or state.

A mover-stayer model was also suggested whereby a fraction of the patients

would always remain in a state whenever they were in it. This would allow

a fraction of addicts to be considered “cured” and another fraction to be

considered “not cured” in spite of the intervention.

*The chapter by Dr. Weng was reviewed by Dr. Greenhouse prior to the technical

review. Dr. Gross reviewed the revised chapter submitted by Dr. Weng and wrote

this summary of the discussion that took place at the meeting.

158
The same transition rates were not assumed in the distinct treatment

groups. In fact, methodology may be developed to test the hypothesis

that the transition rates are equal across the treatment groups, leading

to development of statistical inference techniques for this type of model.

The difficulties that need to be addressed in using this model include (1)

determining the points on the time axis where the parameters change and (2)

how the parameters are to be estimated given the data.

Overall, the model is an excellent beginning for the analysis of this type of

clinical trial data and with modification can be very useful.

AUTHOR

Alan J. Gross, Ph.D.

Professor

Department of Biostatistics, Epidemiology, and Systems Science

Medical University of South Carolina

171 Ashley Avenue

Charleston, SC 29425-2503

159
A Markov Model for NIDA Data on

Treatment of Opiate Dependence*

Mei-Ling Ting Lee

INTRODUCTION

This chapter models the data set collected from the first 17 weeks of the

National Institute on Drug Abuse ARC 090 trial by two-state Markov chains.

For complete data, empirical Bayes procedures are considered. Assuming that

the one-step transition probabilities have independent Beta priors, the posterior

transition probabilities are derived. As a consequence, the expected number of

positive results in a sequence of m + 1 urine samples can be estimated. For

cases where data sets contain missing values, we consider the adjusted

likelihood function obtained by taking into account the k-step transition

probabilities contributed by (k – 1) consecutive missing values and compute

the maximum likelihood estimates (MLEs) for the one-step transition matrix by

the Newton-Raphson method.

COMPLETE DATA

A Two-State Markov Chain

Assume that the sequence of a patient’s urine sample test results, denoted by

X = (X1, . . . ,Xm+1), forms a sequence of Markov-dependent Bernoulli trials,

where Xitakes on values of 0 or 1, representing negative or positive results,

respectively.

Assume that the process is time homogeneous; that is, transition probabilities

are independent of l. Also, assume that 0 < < 1 for all Then,

by the Markov property, the likelihood function based on the sample sequence

*Computer programs used to do the calculations in this chapter are available upon request.

160
of test results of a patient is given by

where nij = { the number of times Xl-1a = i is followed by Xl = j,

l = 2, . . . , m + 1 } is the one-step transition count.

denote the state probabilities of

the k

th test result of a patient. Let p0

 = lim k and p 1 = limk

denote the stationary probabilities of the urine sample testing process of this

patient when the process has achieved statistical equilibrium after a large

number of tests have been taken. Then we have

(2)

If tests are given systematically with an equal number of days between tests,

then the recurrence time can be estimated as follows. Suppose a patient’s urine

sample result is positive at the first trial. Let t denote the recurrence time, that

is, the time of his or her next positive result. That is, X1 = 1,

X2 = . . . = Xt–1 = 0, and Xt = 1. Let T be the random variable of the

recurrence time, then

(3)

Moreover, let denote the number of positive results in a

sequence of m + 1 urine samples from a patient. Then Ym+1 is asymptotically

normal with mean

and variance

(4)

See Cox and Miller (1965) for a review of properties of Markov chains.

An Empirical Bayes Approach

Bayes decision methods for finite-state Markov chains with complete

observations have been discussed by Martin (1967) and Basawa and Prakasa

Rao (1980). We consider in this section empirical Bayes procedures.

161
If results for sequences of m + 1 urine samples are collected from each of the r

patients, chances are that transition probabilities p01 and p10 will vary from

patient to patient. Let U and V denote random variables that correspond to the

respective transition probabilities p01 and p10, which vary across patients. For

simplicity, equation (1) can be rewritten as the following form:

( 1a)

Assume that U and V are independent with prior distributions Beta( ) and

Beta( ), respectively. Let denote their corresponding density

functions. Then we have

where

Hence,

(5)

where

Therefore, the posterior joint density of U and V, given a sample

is of the form

where

162
This implies that the posteriors of U and V are conditionally independent, given

a sample sequence of observations Moreover, the posterior

distribution of U is Beta and the posterior distribution of V

is Beta given X = Hence, the posterior

means and variances of U and V are:

(7a)

(7b)

Employing an empirical Bayes approach, we want to replace in equation (7) the

unknown parameters by their corresponding MLE estimators and

which may be obtained numerically from a likehood function for r patients

based on equation (5).

INCOMPLETE DATA

Maximum Likelihood Estimates

Maximum likelihood methods are commonly used to analyze Markov-chain

data. The asymptotic properties of maximum likelihood estimators and

likelihood ratio tests for complete data have been studied by Anderson and

Goodman (1957) and Billingsley (1961), among others. Aalen and Johansen

(1978) considered nonhomogeneous Markov chains with censored

observations. Keiding and Gill (1990) discussed random truncation models for

Markov processes. Muenz and Rubinstein (1985) discussed cases where

missing values are present. This section investigates the case where there are

missing values in the binary sequence of urine sample results.

Because a transition through (k – 1) consecutive missing values contributes a

k-step transition probability to the observed likelihood, we can calculate the

k-step transition probabilities in terms of elements of the one-step transition

probabilities. Therefore, it is natural to adjust the likelihood function as follows.

Let

163
denote the two-state transition matrix considered in section 2. Then

denotes the matrix of k-step transition probabilities. Let for

i, j = 0, 1, denote the number of transitions from state i to state j with (k – 1)

consecutive missing values in between. Then, conditional on the first test result

the log-likelihood function for an individual can be written as

(8)

where

(9)

To simplify notation, let u, v denote the one-step transition probabilities p01 and

p10, respectively. The conditional log-likelihood function can be expressed as

follows:

where C is a constant.

Estimates for each patient for the maintenance phase of the study are

calculated. MLEs of u and v, denoted by û and can be obtained numerically

by the Newton-Raphson method. Therefore, estimate of the

probability of using opiate of each patient, can be obtained.

164
For weeks 1 through 17, MLE of the probability of using opiate for patients

assigned with buprenorphine, methadone 20 mg, and methadone 60 mg have

means (standard deviation) given by 0.4734 (0.3719), 0.6288 (0.3616) and

0.4970 (0.3157), respectively. These figures are listed in table 1. Note that

patients who have only one urine sample result do not contribute any

information in the study of Markov transition probabilities and, hence, are not

included in the computation.

Due to the fact that there are many cases where the length of the binary

sequence is very short, weighted means of P1 are calculated in table 2. The

weights used in the calculation are the numbers of informative transitions, that

is, transitions that do not begin or end with a missing value, in the sample

sequences. The weighted means of are 0.3664 for buprenorphine, 0.6260

for methadone 20 mg, and 0.4854 for methadone 60 mg.

MLEs of U, V, and P1 vary widely. This phenomenon, however, may be

attributed to the heterogeneity of individuals involved in the study. To take into

account the variability among individuals within each treatment group, an

empirical Bayes approach is undertaken. By adjusting Anderson and

Goodman’s (1957) results for complete data, procedures for testing the

homogeneity for a data set with missing values will be investigated. Censored

cases can be incorporated by modifying Aalen and Johansen’s (1978) method.

This will be done in a subsequent paper.

TABLE 1. Summary statistics for P1. The probability of using opiate.

Method Number of Cases Mean (standard deviation)

Buprenorphine # of cases=50 0.4734 (0.3719)

Methadone 20 mg # of cases=53 0.6288 (0.3616)

Methadone 60 mg # of cases=52 0.4970 (0.3751)

TABLE 2. Summary statistics of P1. The probability of using opiate.

Weighted mean. (The weights used in the calculation are the

numbers of informative transitions in the sample sequences.)

Method Mean (standard deviation)

Buprenorphine 0.3664

Methadone 20 mg 0.6260

Methadone 60 mg 0.4854

165
LIMITATIONS AND DISCUSSION

In the section titled Incomplete Data, random variables U and V are

assumed to have independent Beta priors. Similar empirical Bayes

inferences can be derived if U and V are assumed to have dependent joint

distributions.

An alternative method to incorporate missing values in a Markov model is

to consider the missing value as a third state in the process. Thus, one can

transform the problem into a three-state Markov model with complete data.

In this case independent Dirichlet priors should be used, instead of

independent Beta priors, for entries in the one-step transition probabilities

matrix. It is necessary, however, to justify the randomness of the missing

state.

For a better application of the Markov chain model for urine testings, a

systematic sampling scheme with an equal number of days in between

tests should be planned. This can be done by taking urine samples on

Monday, Wednesday, and Friday for one week and then on Tuesday and

Thursday the next week. Continuing to take samples in this 2-week

alternating pattern will best use the proposed Markov model, which can

handle missing observations for Sunday and Saturday in alternating weeks.

REFERENCES

Aalen, O.O., and Johansen, S. An empirical transition matrix for

nonhomogeneous Markov chains based on censored observations. Scand J

Statist 5:141-150, 1978.

Anderson, T.W., and Goodman, L.A. Statistical inference about Markov chains.

Ann Math Stat 28:89-110, 1957.

Basawa, I.V., and Prakasa Rao, B.L.S. Statistical Inference for Stochastic

Processes. London: Academic Press, 1980.

Billingsley, P. Statistical Inferences for Markov Processes. Chicago: University

of Chicago Press, 1961.

Cox, D.R.. and Miller, H.D. The Theory of Stochastic Processes. London:

Methuen, 1965.

Keiding, N., and Gill, R.D. Random truncation models and Markov processes.

Ann Stat 18:582-602, 1990.

Martin, J.J. Bayesian Decision Problems and Markov Chains. New York: Wiley,

1967.

Muenz, L.R., and Rubinstein, L.V. Markov models for covariate dependence of

binary sequences. Biometrics 41:91-101, 1985.

166
ACKNOWLEDGMENTS

Dr. Ram B. Jain and Dr. Peter A. Lachenbruch made helpful comments.

AUTHOR

Mei-Ling Ting Lee, Ph.D.

Statistics Department

Harvard University

One Oxford Street

Cambridge, MA 02138

167
Summary of Discussion: “A Markov

Model for NIDA Data on Treatment of

Opiate Dependence” by Mei-Ling Ting

Lee*

Alan J. Gross

In her chapter, Dr. Mei-Ling Ting Lee considers a two-state Markov chain to

model urine sample test results in which the outcome IS either positive or

negative for the presence of a particular opiate. At times, study subjects do

not appear for these tests, and as a result, missing values are present in the

data. These missing values are taken into account by adjusting the likelihood

function using Markov properties.

The vector of observations on a given subject is assumed to form a sequence

of Markov-dependent Bernoulli trials with time-independent transition

probabilities, The Markov property allows formation of the likelihood function

based on a sample sequence of test results of a given subject. Maximum

likelihood estimates are obtained for the one-step transition probabilities,

and then, assuming stationarity, an estimate of the stationary drug abuse

probability of each subject is obtained. Since these transition probabilities

vary among subjects, their variability is modeled by assuming that ß priordensity functions govern their behavior. However, this aspect of the research

has not been totally developed. Finally, an estimate for the stationary drug

abuse probability is obtained over each of the three treatment groups.

Some generalizations that may be considered include (1) development of a

three-state model in which the third state is for the missed visits by subjects

(this may be preferable to the present model since missing observations

currently are treated by multiplying the transition matrix to the power

corresponding to the number of consecutive missing observations) and

* The chapter by Dr. Lee was reviewed by Dr. Jewell prior to the technical review.

Dr. Gross reviewed the revised chapter submitted by Dr. Lee and wrote this summary

of the discussion that took place at the meeting.

168
(2) relaxation of time homogeneity and equally spaced observations currently

required in the model.

Some difficulties that exist in applying this model are:

The Markov assumption-that is, the probability an individual tests drug-free

on the current test depends only on whether he or she tested drug-free on

his or her immediate past test-is questionable. One testing drug-free is

likely to have tested drug-free on more than just one previous test, that is,

several tests back.

Much information is likely to lie within the missing data. This aspect of the

model development process is where future efforts should be placed.

If, indeed, the transition probabilities are time homogeneous, then times

between transitions should be roughly exponential. Thus, a test for

exponentiality should be considered to check this assumption.

Concern exists as to whether the data have been sampled for a sufficiently

long period to assume stationarity. At this point, the assumption may be

somewhat optimistic.

Dr. Mei-Ling Lee’s chapter describes an interesting and potentially useful

method for analyzing clinical trial data with this structure. Modifications of

the procedure presented herein, once they are implemented, will lead to an

improved model.

AUTHOR

Alan J. Gross, Ph.D.

Professor of Biostatistics

Department of Biostatistics, Epidemiology, and Systems Science

Medical University of South Carolina

171 Ashley Avenue

Charleston, SC 29425-2503

169
Open/Panel Discussion: Analysis

Issues

Ram B. Jain

Panel Members: Carol K. Redmond (chair), Lloyd D. Fisher, Dean

Follmann, Joel B. Greenhouse, Alan J. Gross, and A.S. Hedayat

The primary issues discussed during this discussion session were:

Statistical approaches to analyze urine data

Validity and importance of craving scores, physician/staff/patient global

scores, and withdrawal symptoms and signs data

Treatment of missing/censored observations

STATISTICAL APPROACHES TO ANALYZE URINE DATA

The following statistical approaches to analyze urine data were discussed:

1. Parametric and nonparametric methods to calculate summary statistics,

for example, estimate of p across clinic visits

2. Model-based, nonsurvival type methods, including those based on

Markovian theory

3. Single- and multiple-failure survival methods

It was mentioned that the statistical approach to analyze urine data would

depend on the nature of the primary outcome variable in the study. A fair

number of participants were in favor of analyzing these data by parametric

model-based approaches (e.g., one proposed by Follmann et al., this volume),

including those using Markovian theory because these models can provide

for (1) explicit consideration of missing/censored observations, (2) inclusion

of covariates representing design and population characteristics, and

(3) consideration of other, for example, sociological variables, which may

170
help to better understand the total phenomenon of drug dependence.

Dr. Hedayat was of the view that if we are interested in implications of our

actions in the future, the model-based approach should be the approach of

choice.

There were others (e.g., Dr. Follmann) who thought that calculation of

summary statistics, such as across-clinic visits, is simple and straightforward

and is sufficient to go through the Food and Drug Administration (FDA)

approval process. According to Dr. Follmann, if a model must be used,

it should be restricted to modeling missing/censored observations.

Correlations and/or interactions between other variables, for example,

correlations between day (Monday vs. Wednesday) of visit and urine

sample results, are not important enough to get the drugs approved by

FDA. Modeling is more suitable to describe patterns of behavior. Dr. Gross

preferred some combination of summary statistics such as p and a model

allowing for covariates where a model would be superimposed on, for example,

p. Dr. Greenhouse was interested in a problem-driven approach. According

to him, heterogeneity is a serious and most important issue in these trials,

and an approach that deals with these kind of issues, for example, one that

is based on Empirical Bayes’ methods (Lee, this volume), would be preferable.

Dr. Jack C. Lee reminded that drug addiction is a chronic condition. He thought

summary statistics and modeling that analyze response are more appropriate

for analyzing data generated by studies in acute conditions. In an area such as

drug dependence, application of survival-type methods should not be summarily

dismissed and should be considered as in other chronic diseases (e.g., cancer)

where it is more important to study survival than response. For Dr. Follmann, it

was more a matter of taste. If survival-type methods are to be considered for

these trials, there would be many remissions and relapses.

There was a fair amount of discussion about the pros and cons of a hypothesistesting vs. a model-based approach for analyzing these trials. Dr. Follmann

and others were in favor of formulating one or more (very) specific primary

hypotheses that will help get the drug approved by FDA. Modeling is more

suitable for describing the pattern of behavior. When reminded that these trials

result in possible multiple endpoints, it was said that as long as hypotheses are

prespecified, be it a (linear) combination of several things and/or variables, it

would be in the best interest of getting a drug approved by FDA. However, if

several endpoints have to be integrated, it should be described in advance

how they would be integrated and the rationale for doing so. Dr. Hedayat

thought that hypothesis testing generates binary (e.g., yes vs. no) results that

are too restricted. He thought that scientifically it is more important to know,

understand, and learn from the process/phenomenon and that this can be done

171
by modeling the process. It was said that FDA has to make a decision and

that a physician, when treating an individual patient, must know whether the

drug works. However, the information that hypothesis testing may provide to

the physician may be too little. He or she not only wants to know whether

or not the drug works but also how, for example, to titrate the drug for different

patients (e.g., a child vs. an adult). Dr. Greenhouse noted that there is a

place for Bayesian and decision theory in designing and analyzing these

trials because these approaches result in meaningful measures such as the

probability of clinically effective response. “These sorts of methods give us

a formalism for doing sensitivity analysis to assess the robustness of our

analyses,” he said. Understanding and learning from the process is important

and necessary for future benefits, but a decision also must be made within the

confines of what is known and knowable now.

There was some discussion about what research should be done to develop

better methods of analyzing these trials. It was felt that the process of missing/

censoring should be modeled. There was also a strong feeling to get more and

better data on those who drop out. When it was mentioned that subjects who

missed three consecutive visits in the ARC 090 study were dropped, Dr. Fisher

said if they had wanted to come back they should have been welcomed back

into the study. This would have generated more data. Dr. Rolley E. Johnson

explained the practical difficulties in putting these people back in the study,

including the problem of titrating them back to their assigned doses, the ethical

problem of putting them back on opiate treatment if they have gone through

the worst part of the withdrawal process, and the possibility of blind being

broken during the period they were out of the trial. There is also the difficulty

of analyzing data on these patients if they are reentered into the trial. Should

the postre entry data on these patients be integrated with the rest of the data?

Or should these data be analyzed separately, and if so, what conclusions can

be drawn from these data? Should the last observation be carried forward for

these patients for the purpose of analyzing the main data set? Some of the

patients who dropped out may not want to come back or should not be allowed

to come back at all because treatment was a failure for them or because

treatment cured them and they did not need the treatment any more.

A suggestion that incentives be built into the design to improve compliance

(i.e., dropout rate) resulted in an involved, informative discussion. Doubts

were raised about the appropriateness of introducing incentives to improve

dropout rates. Incentives may affect the outcome variable itself, in which

case it may not be known whether one is evaluating the effect of incentives

or the treatment. Or there might be an incentive therapy interaction. This

will depend on what the incentives are tied to. For example, if the incentives,

particularly the financial incentives, are tied to producing a negative urine,

172
then it will result in informative missed visits (i.e., a clinic visit might be missed

because a positive urine may be detected), or financial incentive, rather than

treatment, might be the factor to promote absence from drug use. Dr. Fisher

recognized that there might be an interaction between therapy and incentives

and that incentive also may affect compliance, but, “nevertheless, a beneficial

differential drug effect on the top of money would probably mean some sort

of beneficial drug effect.” A concern that different treatment groups may

somehow be imbalanced in terms of incentives received by them could

be rectified if patients can be stratified “on some covariate which would

reflect their propensity or likelihood to take a financial incentive,” said

Dr. Follmann. Dr. Johnson thought that such incentives/contingencies have

the potential to dilute the treatment differences, resulting in prohibitive sample

size requirements. Dr. Peter A. Lachenbruch was concerned about using

financial incentives because this money might end up being used for buying

illegal drugs. Dr. Hedayat insisted on putting more emphasis on characterizing

patient populations to blend the concepts of sampling and design and to

come up with robust designs that minimize natural deficiencies, rather than,

for example, create contingencies to strive for “noise-free” (e.g., dropouts)

experiments. Dr. Gross mentioned that randomized response models that

have a well-developed theory might be suitable for implementing Dr. Hedayat’s

recommendations. However, Dr. Greenhouse reminded that randomized

response models would answer a very limited question in the context of

clinical trials in the drug abuse area.

VALIDITY AND IMPORTANCE OF CRAVING SCORES, PHYSICIAN/STAFF/

PATIENT GLOBAL SCORES, AND WITHDRAWAL SYMPTOMS AND SIGNS

DATA

Dr. Greenhouse suggested that some of these variables may be independent or

explanatory variables, unrelated to the pharmacological effect of the treatment;

as such, they would be time-varying covariates. If so, this presents challenging

statistical analysis problems.

Dr. Fisher expressed that physician/staff/patient global scores are very crude

measures and often do not work. Dr. Michael Murphy replied that,

the approval of Alzheimer’s drugs has now basically stopped

in its tracks because no one has been able to show global

improvement rating. . . . It depends on how one does the

global . . . .

They range from bad to worse, and there is a big controversy right now in the

field as to how one might get at that very useful information.

173
As Dr. Charles Gorodetzky put it, these are difficult-to-measure behavioral

endpoint variables. However, these are the variables that answer questions

such as “what have you done to help the patient?” These are difficult issues,

but they must be dealt with.

A need was felt about some sort of global summary measure that can describe

the status of patients in a global sense, for example, how he or she is doing

after the trial is over. Dr. Nancy L. Geller pointed out that an optimal linear

combination of multiple endpoints can be obtained; that is, a test of missingness

can be combined with a test for efficacy. Weights assigned to different

endpoints can be determined by experts in the field (e.g., cardiologists in

cardiovascular trials). This methodology is very powerful and can detect

relatively smaller differences. However, interpretation of these weighted

summary measures may not always be easy.

Dr. Donald R. Jasinski thought craving scores were not a valid measure of any

form of chemotherapeutic effect and probably had nothing to do with the whole

process of drug dependence. In addition, there was no agreed-on meaning of

craving. “It is probably related to the environment and to learned behavior . . . ,”

Dr. Jasinski said.

Dr. Jasinski was also concerned about moving away from dichotomous

measures to continuous or ordinal scale measures to do some sort of

parametric analysis. He thought all these measures, such as global scores

and symptoms and signs measures, could as well be measured on a binary

scale, which probably would be as meaningful as measuring them on a

continuous or ordinal scale.

Drug dependence is a chronic relapsing disorder. As in other trials of chronic

diseases (e.g., oncology trials), a partial or complete remission (as determined

by urine data) is good enough to show that the drug is efficacious. The key

issue in these trials is to establish pharmacological efficacy. It is very difficult

to show differences in behavioral outcome measures.

TREATMENT OF MISSING/CENSORED OBSERVATIONS

I asked the panel which of the several methods of treating missing/censored

observations presented in the meeting is more acceptable than others. The

methods presented for consideration were estimate, substitute (e.g., by 1),

model, and ignore. Dr. Lee observed estimate, substitute, and ignore to be

different forms of modeling, and as such, modeling and missing at random are

the only alternatives. Dr. Lachenbruch wanted missingness to be considered

as a response by itself.

174
Dr. Fisher recommended doing a sensitivity analysis where different values for

missing/censored observations on a range from zero (a negative sample) to one

(a positive sample) are assumed and different values for different treatments

are assigned. Thus, for each pair of treatment arms, a probability matrix can be

constructed. Each cell of this probability matrix would provide the significance

level, or p value, available from test of treatment differences when specific

pairs of values attached to that cell are assigned to missing/censored

observations for the two treatment groups. From this matrix, a set of pairs

of values (assigned to missing/censored observations) for which one treatment

can be inferred to be better than others can be determined. A professional

judgment then can be made as to whether, under reasonable assumptions for

missing/censored data, one treatment is better. This approach provides for

scenarios under which conclusions could be different.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

175
Open/Panel Discussion: General

Issues

Ram B. Jain

Panel Members: Peter A. Lachenbruch (Cochair), Jack C. Lee (Cochair),

Joseph Collins, Lloyd D. Fisher, Sudhir G. Gupta, Nicholas P. Jewell,

Michael Murphy, Vincent Shu, and Ram C. Tiwari

INTRODUCTION

The issues primarily discussed during this session were:

Need for multiple outcome criteria to deal with various aspects of drug

addiction

High and differential dropout rates and their influence on estimation of

treatment effect

Alternate study designs: comparative dose trials and “enrichment” designs

NEED FOR MULTIPLE OUTCOME CRITERIA TO DEAL WITH VARIOUS

ASPECTS OF DRUG ADDICTION

Almost all the participants at the meeting agreed that there is a need for

multiple outcome criteria in these trials. However, what should be measured

should be clearly defined. Dr. Murphy would definitely incorporate urine

screens as a measure in his studies, particularly because it would be easy to

standardize this measure across the centers. However, this would not be the

key, pivotal outcome in his studies because this measure is of “questionable

clinical relevance.” He would like to study the impact of urine screens “on

the sites we select, the patients we enroll, the numbers of patients we enroll,

and how often we can retain them.” If the patients become free of opiates

but substitute opiates by using other illicit drugs like Valium, cocaine,

amphetamine, or marijuana, he would consider this a failure of (opiate)

treatment. This substitution of other drugs for opiates should be factored into

data analysis.

176
Dr. Gupta warned against having too many outcome measures because

correlations between these measures must be considered in the analysis.

Too many measures make the problem multidimensional and too complicated.

Obtaining a clear, solid conclusion from the trial is important. However,

because the effect of (opiate) treatment drugs lasts for only a limited

time–24 hours or so-he was in favor of analyzing data collected on each

day separately. According to Dr. Jewell, the primary interest should be

evaluating whether the patient has improved since the treatment began,

and as such, treating multiple observations from a patient as anything more

than a single data point should not be done.

There was no consensus at the meeting about how to handle the data on

multiple outcome variables. Dr. Murphy was in favor of integrating data from

urine screens with other measures into an overall index of disease severity.

He liked the idea of collapsing across measures. Dr. Collins wanted each

measure to be analyzed separately because, in general, investigators may

be interested in knowing exactly on which measures what the direction and

magnitude of treatment differences are, if any exist. A drug may reduce the

opiate abuse but may have a problem in retaining patients on the treatment.

On the other hand, a drug may not be so effective in reducing the frequency

of drug abuse but may be very effective retaining patients on the treatment.

The investigator should be the one to make a final decision about the

usefulness of the proposed treatment.

However, as Dr. Fisher pointed out, if there are too many outcome measures,

it is more than likely that the direction and magnitude of treatment differences

on these variables will be different at different levels. This could be a potential

source of confusion and indecision for the investigator. It would only be helpful

if a composite measure is obtained from different outcome measures. The

analysis of this combined measure should be helpful in deciding if the drug

has an overall effect. Subsequently, individual measures can be analyzed

and evaluated. I suggested that an investigator be asked at the beginning

of a trial about the performance required on each outcome measure for the

proposed drug to be minimally useful and/or successful. For example, for the

proposed drug to be useful and/or successful, patients must participate in the

study for at least 4 weeks, should have at least 75 percent negative urines,

and should have a craving score of no more than 50 on at least 75 percent

of their clinic visits. The performances on different measures for each patient

can then be combined to obtain some sort of combined score without statistical

manipulations. These combined scores can then be subjected to formal

analysis.

177
Dr. Fudala did not think a single composite score would be clinically meaningful.

Dr. Shu expressed the need for a more focused study and the need for defining

a primary outcome measure, for example, the reduction in incidence of drug

abuse. Other secondary measures, such as rating scales to measure patients’

physical or psychological dependence on drugs, can be developed. Craving

scores, a nonthreatening measure, can also be used. Correlations between

craving scores and incidence of drug abuse can be studied. The bias in

obtaining some of the soft measures can be reduced and/or eliminated if

blinded evaluating physicians, separated from treating physicians, take these

measures.

As Dr. Geller put it, there are likely to be situations where combining several

measures (test statistics) would be appropriate, and in some cases, it would

be more appropriate to have one primary and several secondary measures

(statistics).

HIGH AND DIFFERENTIAL DROPOUT RATES AND THEIR INFLUENCE ON

ESTIMATION OF TREATMENT EFFECT

Almost all participants were concerned about the high dropout rates in these

trials. Dr. Jewell thought, with that much missing/dropout data “one can say

anything about treatment effect.” In “a trial of this kind . . . where 80 percent

of the patients on placebo were not available with regard to any kind of outcome

or restricted . . . outcome, there is just no way one would be able to make

sense of what that meant with regard to an active drug . . . .” He advised that

pilot studies that concentrate on the ability to collect outcome data of specified

kinds be conducted so that, for instance, specific patient populations available

for specific treatments and followup can be identified.

There was an agreement that high and differential dropout rates for different

reasons in different treatment groups can compromise estimation of treatment

effects. For example, the drugs may “cure” certain patients, and as such, they

do not need treatment anymore (and they drop out). In other cases, the drug

may be a failure, and as such, the patients do not come back. Some patients

may drop out because of toxicity even if the drug was working for them. Other

times the pattern of dropouts may be related to covariates such as age, sex,

and marital status.

In the opinion of Dr. Gupta, dropout rates may contain information about the

treatment effect, and as such, dropout rates should be analyzed as a separate

outcome variable in addition to other variables related to the improvement in the

condition of patients. Dr. Jack C. Lee also said, “. . . if the missingness has any

valuable information for the relevance of the outcome variable, which I think in

178
this case is, then make it a part of the analysis . . . .” According to Dr. Murphy,

only legitimate discontinuation from the study is due to toxicity. Dropouts have

“only a fraction to do with the therapeutic intervention in place. . . . it is an issue

of staff investment.” Clinical staff should prevent that from happening. Dr.

Johnson commented that an administrative dropout after three consecutive

missed visits may be one of the reasons for a large dropout rate in the ARC

090 trial, but “. . . when you don’t put a restriction on with medications that have

physical dependence-producing properties you bring in a lot of complications

that I don’t know how you deal with . . . .” Dr. Follmann suggested that efforts

could have been made to collect urine samples from the patients even after

they were out of the trial. Dr. Johnson retorted that they (patients) could have

been paid for coming back to provide urine samples but that a provision like

that would constitute payment for dropping out of the trial, which brings in an

ethical problem because these payments could be used to buy drugs of abuse.

Dr. Johnson remarked, “. . . how do you get people back when they did not

come to begin with?” Missed visits is an inherent phenomenon in these patient

populations.

It was suggested that sensitivity analysis recommended by Dr. Fisher and the

approaches proposed by Drs. Weng (this volume) and Follmann and colleagues

(this volume) are promising tools to adjust for missing/censored data.

ALTERNATE STUDY DESIGNS

Comparative Dose Trials

Most of the participants recognized the usefulness of comparative dose trials.

However, two issues must be dealt with in these kinds of designs. First, the

selection of doses should be done carefully. As Dr. Murphy said, “Early in the

development especially, it is very difficult to judge where one is on the dose

effect curve. One could be asymptotically too high or too low.” Dr. Shu

suggested the physicians should be allowed to titrate in the first studies to

select the doses they feel comfortable with, and these selected doses can be

used in dose comparison trials. The second difficulty in doing these kinds of

trials lies in that, in the neuropsychiatric area, the effect sizes are very small.

Relatively large sample sizes may be required to detect differences between

these small effects for different treatment groups.

However, Dr. Fisher was, in general, not in favor of doing forced dose

escalation studies.

179
“ENRICHMENT” DESIGNS

It would be of interest to physicians to minimize the damage to those who

cannot benefit from a proposed new therapy. Those who can benefit probably

can be identified from those who cannot in a double blind trial where everybody

receives medication. Then, in a random double blind second (e.g., dose

comparison) trial, or probably the second phase of the same trial, only the

responders can be studied. At the request of Dr. Donald F. Klein, professor of

psychiatry at the College of Physicians and Surgeons of Columbia University, I

asked the participants to comment on the usefulness of such designs in the

drug abuse area.

Dr. Jewell thought the main idea behind these kinds of designs is to identify

subgroups based on some sort of covariate information that amounts to

evaluation of interaction effects. If so, these trials could result in large sample

size requirements. Dr. Fisher said that these trials are initiated when physicians

intuitively feel that some substrata of patient population are biologically and/or

psychologically so different from the others that for some there is no hope,

whereas others can respond. This is an efficient way to show activity. As Dr.

Jack C. Lee said, these designs can be useful in determining the profiles of the

drug addicts who respond. This information can then be used to determine

eligibility for future studies. These designs can be used to demonstrate

heterogeneity between responders and nonresponders, but this heterogeneity,

if present, has to be rooted, in Dr. Murphy’s opinion, in some sort of biological

substrate. It should flow from theory into practice.

Several participants expressed reservations and struck a note of caution

about the use of “enrichment” designs. The analysis of these designs is

difficult because of, among other things, possible carryover effects. The

interpretation of results obtained by analyzing these trials presents serious

challenges. Dr. Vocci presented two examples where one can incorrectly

conclude that an alternate medication is ineffective. “If you give an agonist

and find out who responds to the agonist, and then you are testing an agonist

in an enrichment design vs. a partial agonist, what you may be doing is

undermedicating the patients with partial agonist and making ii look worse . . . .

A study was done in which anxiety patients were tested for benzodiazepine

receptor, benzodiazepine sensitivity, if they were actually helped by

benzodiazepine, and then they were randomized to the same benzodiazepine

or a nonbenzodiazepine, and what happened was the patients who were

randomized to the nonbenzodiazepine had this mild withdrawal, which was

not helped by the new agent, and many of them dropped out as a result. . . .

This withdrawal syndrome actually exacerbated their anxiety.” Dr. Greenhouse

presented a similar example from a trial done in the psychiatric area.

180
Consequently, although enrichment designs do have a place in the drug

development process (particularly when a new chemical entity is being studied),

where a post hoc analysis of the data will be meaningful in identifying easily

discernible (by the average physician), clinically relevant baseline variables that

separate responders from nonresponders, prospectively, that “good” group

should be studied in a traditional clinical trial.

AUTHOR

Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

181
Technical Review Committee Meeting:

Statistical Issues in Clinical Trials for

Treatment of Opiate Dependence

Medications Development Division

National Institute on Drug Abuse

December 2-3, 1991

List of Participants

Jack D. Blaine, M.D.

Chief

Treatment Research Branch

Division of Clinical Research

National Institute on Drug Abuse

Parklawn Building, Room 10A-30

5600 Fishers Lane

Rockville, MD 20857

Robert J. Chiarello, M.D.

Medical Officer

Treatment Research Branch

Division of Preclinical Research

National Institute on Drug Abuse

Parklawn Building, Room 10A-30

5600 Fishers Lane

Rockville, MD 20857

Joseph Collins, Sc.D.

Chief

Cooperative Studies Program

Coordinating Center, 151E

Department of Veterans Affairs Medical

Center

Perry Point, MD 21902

Edward J. Cone, Ph.D.

Chief

Laboratory of Chemistry and Drug

Metabolism

Addiction Research Center

National Institute on Drug Abuse

P.O. Box 5180

Baltimore, MD 21224

Sandra L. Dickerson, B.S.

Medical Technologist

Addiction Research Center

National Institute on Drug Abuse

P.O. Box 5180

Baltimore, MD 121224

Lloyd D. Fisher, Ph.D.

Professor

Department of Statistics

SC-32

University of Washington

19220 64th Place, N.E.

Seattle, WA 98155

182
Dean Follmann, Ph.D.

Mathematical Statistician

Biostatistics Research Branch

National Heart, Lung, and Blood

Institute

Federal Building, Room 2A11

Bethesda, MD 20892

Paul J. Fudala, Ph.D.

Assistant Professor

Department of Psychiatry

University of Pennsylvania School of

Medicine and the Department of

Veterans Affairs Medical Center

Building 15

University and Woodland Avenues

Philadelphia, PA 19104

Nancy L. Geller, Ph.D.

Chief

Biostatistics Research Branch

National Heart, Lung, and Blood

Institute

Federal Building, Room 2All

Bethesda, MD 20892

Albert J. Getson, Ph.D.

Associate Director

Merck Clinical Biostatistical Research

Labs

BL 3-2

West Point, PA 19486

Harold Gordon, Ph.D.

Project Officer

Division of Epidemiology and

Prevention Research

National Institute on Drug Abuse

5600 Fishers Lane

615 Rockwall II

Rockville, MD 20852

David A. Gorelick, M.D., Ph.D.

Chief

Treatment Research Branch

Addiction Research Center

National Institute on Drug Abuse

P.O. Box 5180

4940 Eastern Avenue

Baltimore. MD 21224

Charles W. Gorodetzky, M.D., Ph.D.

Executive Director

CNS Drug Development

CIBA-Geigy Corporation

556 Morris Avenue

Summit, NJ 07901

Joel B. Greenhouse, Ph.D.

Associate Professor

Department of Statistics

Carnegie-Mellon University

5000 Forbes Avenue

Pittsburgh, PA 15213-3890

Alan J. Gross, Ph.D.

Professor

Department of Biostatistics,

Epidemiology, and Systems Science

Medical University of South Carolina

College of Graduate Studies

171 Ashley Avenue

Charleston, SC 29425-2503

Charles V. Grudzinskas, Ph.D.

Director

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

Sudhir C. Gupta, Ph.D.

Associate Professor

Statistics Department

Northern Illinois University

DeKalb. IL 60115-2888

AS. Hedayat, Ph.D.

Professor

Department of Mathematics, Statistics,

and Computer Sciences, MC249

University of Illinois

P.O. Box 438

Chicago, IL 60680

John Hyde, M.D., Ph.D.

Medical Officer

Pilot Drug Evaluation Division, HFD-007

Food and Drug Administration

5600 Fishers Lane

Rockville, MD 20857

183
Ram B. Jain, Ph.D.

Mathematical Statistician

Biometrics Branch

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

Donald R. Jasinski, M.D.

Chief

Center for Chemical Dependence

Francis Scott Key Medical Center

4940 Eastern Avenue A-l-East

Baltimore, MD 21224

Nicholas P. Jewell, Ph.D.

Professor of Biostatistics

University of California at Berkeley

School of Public Health

Berkeley, CA 94720

Rolley E. Johnson, Pharm.D.

Assistant Professor

Department of Psychiatry and

Behavioral Sciences

Johns Hopkins School of Medicine

Building G, Room 2725

85510 Nathan Shock Drive

Baltimore, MD 21224

William F. Krol, Ph.D.

Chief

Statistical Programming Section, 151E

Department of Veterans Affairs Medical

Center

Perry Point, MD 21902

Peter A. Lachenbruch, Ph.D.

Professor of Biostatistics

University of California, Los Angeles

School of Public Health

Los Angeles, CA 90024-1772

Young Jack C. Lee, Ph.D.

Chief

Biometry and Mathematical Statistics

Branch

National Institute of Child Health and \

Human Development

National Institutes of Health

Executive Plaza North, Room 630

Bethesda, MD 20892

Mei-Ling Ting Lee, Ph.D.

Assistant Professor

Mathematics Department

Boston University

111 Cummington Street

Boston, MA 02215

Shou-Hua Li, Ph.D.

Statistician

Biometrics Unit, EODPP

Westwood Building, Room 533

National Institute of Dental Research

Bethesda, MD 20892

Michael Murphy, M.D.

Medical Director

Neurosciences—SBU

Hoechst Roussel Pharmaceutical, Inc.

Route 202-206 North

Sommerville, NJ 08876-1258

Taesung Park, Ph.D.

Mathematical Statistician

National Institute of Child Health and

Human Development

National Institutes of Health

Executive Plaza North, Room 630

Bethesda. MD 20892

Carol K. Redmond, Ph.D.

Professor

Department of Biostatistics

University of Pittsburgh

318 Parran Hall

Pittsburgh, PA 15261

184
Saul Rosenberg, Ph.D.

Mathematical Statistician

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville. MD 20857

Vincent Shu, Ph.D.

Section Head

Clinical Statistics and System

Development

D436 APGC

Abbott Laboratories

One North Abbott Park Road

Abbott Park, IL 60064

Richard Stein, Ph.D.

Mathematical Statistician

Food and Drug Administration

HFD-007, Room 9B45

5600 Fishers Lane

Rockville, MD 20857

Ram C. Tiwari, Ph.D.

Associate Professor

Department of Mathematics

University of North Carolina at Charlotte

Charlotte, NC 28223

Frank J. Vocci, Ph.D.

Deputy Director

Medications Development Division

National Institute on Drug Abuse

Parklawn Building, Room 11A-55

5600 Fishers Lane

Rockville, MD 20857

L.J. Wei, Ph.D.

Professor

Department of Biostatistics

Harvard School of Public Health

677 Huntington Avenue

Boston, MA 02115

T.S. Weng, Ph.D.

Mathematical Statistician

Division of Biometric Sciences

Office of Science and Technology

Center for Devices and Radiological

Health

Food and Drug Administration

Suite 405

1801 Rockville Pike

Rockville, MD 20852

Curtis Wright, M.D.

Medical Officer

Pilot Drug Evaluation Division

Food and Drug Administration

5600 Fishers Lane

Rockville, MD 20852

Margaret Wu, Ph.D.

Mathematical Statistican

Biostatistics Research Branch

National Heart, Lung, and Blood

Institute

National Institutes of Health

Federal Building, Room 2A11

Bethesda, MD 20892

185
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85 EPIDEMIOLOGY OF INHALANT ABUSE: AN UPDATE. Raquel A. Crider,

Ph.D., and Beatrice A. Rouse, Ph.D., eds.

GPO Stock #017-024-01360-9 $5.50 NTIS PB #89-123178/AS $31

86 COMPULSORY TREATMENT OF DRUG ABUSE: RESEARCH AND

CLINICAL PRACTICE. Carl G. Leukefeld, D.S.W., and Frank M. Tims, Ph.D.,

eds.

GPO Stock #017-024-01352-8 $7.50 NTIS PB #89-151997/AS $31

87 OPIOID PEPTIDES: AN UPDATE. Rao S. Rapaka, Ph.D., and Bhola N.

Dhawan, M.D., eds.

GPO Stock #017-024-01366-8 $7 NTIS PB #89-158430/AS $45

88 MECHANISMS OF COCAINE ABUSE AND TOXICITY. Doris H. Clouet,

Ph.D.; Khursheed Asghar, Ph.D.; and Roger M. Brown, Ph.D., eds.

GPO Stock #017-024-01359-5 $11 NTIS PB #89-125512/AS $39

89 BIOLOGICAL VULNERABILTY TO DRUG ABUSE. Roy W. Pickens,

Ph.D., and Date S. Svikis, B.A., eds.

GPO Stock #017-022-01054-2 $5 NTIS PB #89-125520/AS $23

188
90 PROBLEMS OF DRUG DEPENDENCE 1988: PROCEEDINGS OF THE

50TH ANNUAL SCIENTIFIC MEETING, THE COMMITTEE ON PROBLEMS

OF DRUG DEPENDENCE, INC. Louis S. Harris, Ph.D., ed.

GPO Stock #017-024-01362-5 $17

91 DRUGS IN THE WORKPLACE: RESEARCH AND EVALUATION DATA.

Steven W. Gust, Ph.D., and J. Michael Walsh, Ph.D., eds.

GPO Stock #017-024-01384-6 $10 NTIS PB #90-147257/AS $39

92 TESTING FOR ABUSE LIABILITY OF DRUGS IN HUMANS. Marian W.

Fischman, Ph.D., and Nancy K. Mello, Ph.D., eds.

GPO Stock #017-024-01379-0 $12 NTIS PB #90-148933/AS $45

93 AIDS AND INTRAVENOUS DRUG USE: FUTURE DIRECTIONS FOR

COMMUNITY-BASED PREVENTION RESEARCH. C.G. Leukefeld, D.S.W.;

R.J. Battjes, D.S.W.; and Z. Amsel, DSc., eds.

GPO Stock #017-024-01388-9 $10 NTIS PB #90-148941/AS $39

94 PHARMACOLOGY AND TOXICOLOGY OF AMPHETAMINE AND

RELATED DESIGNER DRUGS. Khursheed Asghar, Ph.D., and Errol De

Souza, Ph.D., eds.

GPO Stock #017-024-01386-2 $11 NTIS PB #90-148958/AS $39

95 PROBLEMS OF DRUG DEPENDENCE 1989: PROCEEDINGS OF THE

51ST ANNUAL SCIENTIFIC MEETING, THE COMMITTEE ON PROBLEMS

OF DRUG DEPENDENCE, INC. Louis S. Harris, Ph.D., ed.

GPO Stock #017-024-01399-4 $21 NTIS PB #90-237660/AS $67

96 DRUGS OF ABUSE: CHEMISTRY, PHARMACOLOGY, IMMUNOLOGY,

AND AIDS. Phuong Thi Kim Pham, Ph.D., and Kenner Rice, Ph.D., eds.

GPO Stock #017-024-01403-6 $8 NTIS PB #90-237678/AS $31

97 NEUROBIOLOGY OF DRUG ABUSE: LEARNING AND MEMORY. Lynda

Erinoff, Ph.D., ed.

GPO Stock #017-024-01404-4 $8 NTIS PB #90-237686/AS $31

98 THE COLLECTION AND INTERPRETATION OF DATA FROM HIDDEN

POPULATIONS. Elizabeth Y. Lambert, MS., ed.

GPO Stock #017-024-01407-9 $4.75 NTIS PB #90-237694/AS $23

99 RESEARCH FINDINGS ON SMOKING OF ABUSED SUBSTANCES.

C. Nora Chiang, Ph.D., and Richard L. Hawks, Ph.D., eds.

GPO Stock #017-024-01412-5 $5 NTIS PB#91-141119 $23

189
100 DRUGS IN THE WORKPLACE: RESEARCH AND EVALUATION DATA.

VOL. II. Steven W. Gust, Ph.D.; J. Michael Walsh, Ph.D.; Linda B. Thomas,

B.S.; and Dennis J. Crouch, M.B.A., eds.

GPO Stock #017-024-01458-3 $8

101 RESIDUAL EFFECTS OF ABUSED DRUGS ON BEHAVIOR. John W.

Spencer, Ph.D., and John J. Boren, Ph.D., eds.

GPO Stock #017-024-01426-7 $6 NTIS PB #91-172858/AS $31

102 ANABOLIC STEROID ABUSE. Geraline C. Lin, Ph.D., and Lynda Erinoff,

Ph.D., eds.

GPO Stock #017-024-01425-7 $8 NTIS PB #91-172866/AS $31

103 DRUGS AND VIOLENCE: CAUSES, CORRELATES, AND

CONSEQUENCES. Mario De La Rosa, Ph.D.; Elizabeth Y. Lambert, M.S.;

and Bernard Gropper, Ph.D., eds.

GPO Stock #017-024-01427-3 $9 NTIS PB #91-172841/AS $31

104 PSYCHOTHERAPY AND COUNSELING IN THE TREATMENT OF

DRUG ABUSE. Lisa Simon Onken, Ph.D., and Jack D. Blaine, M.D., eds.

GPO Stock #017-024-01429-0 $4 NTIS PB #91-172874/AS $23

105 PROBLEMS OF DRUG DEPENDENCE, 1990: PROCEEDINGS OF THE

52ND ANNUAL SCIENTIFIC MEETING, THE COMMITEE ON PROBLEMS

OF DRUG DEPENDENCE, INC. Louis S. Harris, Ph.D.. ed.

GPO Stock #017-024-01435-4 $22

106 IMPROVING DRUG ABUSE TREATMENT. Roy W. Pickens, Ph.D.; Carl

G. Leukefeld, D.S.W.; and Charles R. Schuster, Ph.D., eds.

GPO Stock #017-024-01439-7 $12 NTIS PB #92-105873

Paperback $50 Microfiche $19

107 DRUG ABUSE PREVENTION INTERVENTION RESEARCH:

METHODOLOGICAL ISSUES. Carl G. Leukefeld, D.S W., and William J.

Bukoski, Ph.D., eds.

GPO Stock #017-024-01446-0 $9 NTIS PB #92-160985

Paperback $35 Microfiche $17

108 CARDIOVASCULAR TOXICITY OF COCAINE: UNDERLYING

MECHANISMS. Pushpa V. Thadani, Ph.D., ed.

GPO Stock #017-024-01446-0 $7 NTIS PB #92-106608

Paperback $35 Microfiche $17

190
109 LONGITUDINAL STUDIES OF HIV INFECTION IN INTRAVENOUS DRUG

USERS: METHODOLOGICAL ISSUES IN NATURAL HISTORY RESEARCH.

Peter Hartsock, Dr.P.H., and Sander G. Genser, M.D., M.P.H., eds.

GPO Stock #017-024-01445-1 $4.50 NTIS PB #92-106616

Paperback $26 Microfiche $12.50

110 THE EPIDEMIOLOGY OF COCAINE USE AND ABUSE. Susan Schober,

Ph.D., and Charles Schade, M.D., M.P.H., eds.

GPO Stock #017-024-01456-7 $11 NTIS PB #92-14624-0

Paperback $43 Microfiche $17

111 MOLECULAR APPROACHES TO DRUG ABUSE RESEARCH VOLUME I:

RECEPTOR CLONING, NEUROTRANSMITTER EXPRESSION, AND

MOLECULAR GENETICS. Theresa N.H. Lee, Ph.D., ed.

Not for sale at GPO NTIS PB #92-135743

Paperback $35 Microfiche $17

112 EMERGING TECHNOLOGIES AND NEW DIRECTIONS IN DRUG

ABUSE RESEARCH. Rao S. Rapaka, Ph.D.; Alexandros Makriyannis, Ph.D.;

and Michael J. Kuhar, Ph.D., eds.

GPO Stock #017-024-01455-9 $11

113 ECONOMIC COSTS, COST-EFFECTIVENESS, FINANCING, AND

COMMUNITY-BASED DRUG TREATMENT. William S. Cartwright, Ph.D.,

and James M. Kaple, Ph.D., eds.

Not for sale at GPO NTIS PB #92-155795

Paperback $35 Microfiche $17

114 METHODOLOGICAL ISSUES IN CONTROLLED STUDIES ON EFFECTS

OF PRENATAL EXPOSURE TO DRUG ABUSE. M. Marlyne Kilbey, Ph.D., and

Khursheed Asghar, Ph.D., eds.

GPO Stock #017-024-01459-1 $12 NTIS PB #92-146216

Paperback $43 Microfiche $17

115 METHAMPHETAMINE ABUSE: EPIDEMIOLOGIC ISSUES AND

IMPLICATIONS. Marissa A. Miller, D.V.M., M.P.H., and Nicholas J. Kozel, MS.,

eds.

GPO Stock #017-024-01460-5 $4

116 DRUG DISCRIMINATION: APPLICATIONS TO DRUG ABUSE

RESEARCH. Richard A. Glennon, Ph.D.; Torbjörn U.C. Järbe, Ph.D.; and

Jerry Frankenheim, Ph.D., eds.

GPO Stock #017-024-01470-2 $13

191
117 METHODOLOGICAL ISSUES IN EPIDEMIOLOGICAL, PREVENTION,

AND TREATMENT RESEARCH ON DRUG-EXPOSED WOMEN AND THEIR

CHILDREN. M. Marlyne Kilbey, Ph.D., and Khursheed Asghar, Ph.D., eds.

GPO Stock #017-024-01472-9 $12

118 DRUG ABUSE TREATMENT IN PRISONS AND JAILS. Carl G.

Leukefeld, D.S.W., and Frank M. Tims, Ph.D., eds.

GPO Stock #017-024-01473-7 $16

119 PROBLEMS OF DRUG DEPENDENCE 1991: 53RD ANNUAL

SCIENTIFIC MEETING, THE COMMITTEE ON PROBLEMS OF DRUG

DEPENDENCE, INC. Louis S. Harris, Ph.D., ed.

GPO Stock #017-024-01474-5 $22

120 BIOAVAILABILITY OF DRUGS TO THE BRAIN AND THE BLOODBRAIN BARRIER. Jerry Frankenheim, Ph.D., and Roger M. Brown, Ph.D., eds.

121 BUPRENORPHINE: AN ALTERNATIVE TREATMENT FOR OPIOID

DEPENDENCE. Jack D. Blaine, Ph.D., ed.

122 RESEARCH METHODS IN WORKPLACE SETTINGS. Helen Axel, M.A.,

and Dennis J. Crouch, M.B.A., eds.

123 ACUTE COCAINE INTOXICATION: CURRENT METHODS OF

TREATMENT. Heinz Sorer, Ph.D., ed.

124 NEUROBIOLOGICAL APPROACHES TO BRAIN-BEHAVIOR

INTERACTION. Roger M. Brown, Ph.D., and Joseph Frascella, Ph.D., eds.

125 ACTIVATION OF IMMEDIATE EARLY GENES OF ABUSE. Reinhard

Grzanna, Ph.D., and Roger M. Brown, Ph.D., eds.

126 MOLECULAR APPROACHES TO DRUG ABUSE RESEARCH VOLUME

II: STRUCTURE, FUNCTION, AND EXPRESSION. Theresa N.H. Lee, Ph.D.,

ed.

192
DHHS Publication No. (ADM) 92-1947

Alcohol, Drug Abuse, and Mental Health Admnistration

Printed 1992