Treatment of Drug Users
The past decade has seen a wealth of new research-based resources for drug and alcohol treatment providers. Numerous scholarly reviews of various aspects of the treatment literature were published in the 1990s (e.g., Anglin and Hser, 1990; Carroll, 1996; Higgins, 1999; Meyer, 1992; O’Brien, 1996; Platt, 1995; Van Horn and Frank, 1998). In addition, the decade saw a succession of consensus statements on the state of the science of drug treatment, produced by blue-ribbon panels of experts convened by the Institute of Medicine (1990, 1995, 1996, 1998), the Office of National Drug Control Policy (1996, 1998), the American Psychiatric Association (1995), and the National Institutes of Health (National Consensus Development Panel on Effective Medical Treatment of Opiate Addiction, 1998). The National Institute on Drug Abuse (1999) recently produced an accessible 54-page guide to research-based principles of drug addiction treatment. And the Center for Substance Abuse Treatment now distributes Treatment Improvement Protocols, providing best-practice guidelines for drug abuse treatment (see http://www.treatment.org/Externals/tips.html).
We make no attempt in this chapter to review the substantive findings of the growing empirical literature on drug treatment outcomes. Our task is somewhat different. We articulate here recommendations for continuous improvement of the science of drug treatment. In particular, there is a need for better information on the potential benefits and costs of drug treatment as an adjunct to, or an alternative to, traditional criminal justice sanctions and coerced treatment regimes.
Reviewing the evidence, we conclude that the randomized controlled trial has not yet been used to full advantage in treatment evaluation research. Other reviews have stressed the clear value of non-experimental observational studies to evaluate treatment. Without gainsaying the value of these studies, this committee’s emphasis is different. Some very informative randomized control trials have been completed, but more trials are needed to fill gaps in evidence that cannot be filled definitively with nonexperimental studies. This chapter reviews the research literature with special emphasis on this important gap.
Information Needed for Policy Guidance
We begin with three observations about the kinds of information that policy makers need.
First, there is no single entity or process called “drug treatment.” Rather, there are a plethora of therapies, modalities, and delivery systems: public and private, in-patient and outpatient, voluntary and coerced, talk-based and psychopharmacological, individual and group, cognitive and behavioral, and so on. Clients, family members, and practitioners need guidance as to the most effective strategies for a given client and setting, at an affordable cost. Policy makers and treatment funders need guidance as to the most cost-effective strategies or combinations of strategies.
Second, a very large fraction of the most heavily involved drug users come into contact with the criminal justice system, and many are incarcerated or under the supervision of probation or parole officers. For example, in 1996, 24 percent of jail inmates reported using cocaine or crack in the month before their most recent offense; 9 percent reported heroin or opiate use, and 10 percent reported stimulant use (Sourcebook of Criminal Justice Statistics, 1998, Table 6.33, http://www.albany.edu/sourcebook/1995/pdf/t633.pdf). Policy makers need better information on the benefits of drug treatment as an adjunct to, or an alternative to, traditional criminal justice sanctions.
Third, somewhere between 3.5 and 6.7 million people in the United States are in need of effective drug treatment (see Woodward et al., 1997; Epstein and Gfroerer, 1995). Only a minority of those who need drug treatment are currently receiving it—somewhere between 20 percent (Lamb et al., 1998) and 48 percent (Woodward et al., 1997). Fewer than 200,000 individuals currently receive methadone maintenance,1 yet it is believed that there are 600,000 to 1,000,000 heroin addicts in the United
States (Wright et al., 1997). Policy makers urgently need to know the feasibility and possible benefit of expanding the size and coverage of the drug treatment system to reach individuals not currently receiving treatment.
With these points in mind, we offer in this chapter recommendations for continuous improvement of the science of drug treatment, but also for improved estimation of drug treatment effect sizes to support cost-effectiveness and benefit-cost analyses that can inform policy makers. Both goals require increased attention to potential threats to the validity of inferences from treatment outcome studies.
Rationale for Treatment Interventions
When complete and permanent abstinence is used as a criterion of success, between 60 and 90 percent of clients relapse to drug use within 12 months of treatment; relapse rates are similarly high for tobacco and alcohol treatment (Phillips, 1987). Thus, many outside the treatment community have expressed skepticism about the benefits of funding drug treatment.
To some extent, this skepticism is based on unrealistic expectations. In addition to their drug abuse, heavy drug users frequently suffer from various other “co-morbid” conditions—other mental and physical health problems, economic and family problems—that greatly complicate treatment. Moreover, epidemiological, behavioral, genetic, and neuropsychological research suggest that many of those at highest risk for drug dependence and other patterns of antisocial behavior show early and persistent deficits of cognitive functioning and impulse control that may reflect neurological deficits (e.g., Moffitt, 1993). Finally, as we note in Chapter 2, it has become clear that psychoactive drugs have profound and possibly chronic effects on brain functioning, which leaves the person biologically vulnerable to relapse long after the immediate signs of addiction have been alleviated (Leshner, 1997).
Thus, drug dependence is increasingly seen as a chronic relapsing brain disorder (O’Brien and McLellan, 1996; Leshner, 1997), for which
According to the Treatment Episodes Data Set (TEDS), heroin and other opiates accounted for 16 percent of the approximately 1.5 million annual treatment admissions in 1997—the largest category of admissions (Substance Abuse and Mental Health Services Administration, 1999, http://www.samhsa.gov/oas/TEDS/TEDSReport97.pdf). Of these, 42 percent (approximately 100,000) were assigned to methadone maintenance treatment. The Uniform Facility Data Set (Substance Abuse and Mental Health Services Administration, 1997, p. 36) indicates that 138,000 of all clients in treatment (15 percent) were receiving either methadone or LAAM. The American Methadone Providers Association cites a higher figure on the number of people currently on methadone maintenance: 170,000.
permanent abstinence may not a realistic goal of any single round of treatment for heavy long-term users. From this perspective, drug dependence requires long-term management comparable to those of other chronic relapsing disorders, such as hypertension, diabetes, and asthma. Drug treatment is a fairly modest intervention relative to the history of conditioned associations, situational stressors, and peer supports that reinforce a pattern of drug use. Thus, without major neuropharmacological breakthroughs, it is unrealistic to expect treatment to provide dramatic short-term results.
At the same time, claims for the effectiveness of drug treatment are sometimes based on misleading or ambiguous results. Many authors have cited observational studies comparing pretreatment and posttreatment drug use consistently find that between a quarter and a half of clients show significant reductions in their frequency of drug use. These reductions are interpreted as evidence for the effectiveness of drug treatment. The U.S. General Accounting Office (1998) has argued persuasively that the heavy reliance on self-report outcome measures in treatment outcome research may inflate estimates of the effectiveness of drug treatment. In this chapter, we argue that these estimates are often vulnerable to various other methodological biases.
A common argument is that even if drug treatment has less than perfect success rates, it is still a good investment. Many authors have cited the CALDATA estimate (Gerstein et al., 1994) that drug treatment has a benefit-cost ratio in the $3 to $7 range, or RAND’s analysis (Rydell and Everingham, 1994) suggesting that it is considerably cheaper to reduce cocaine use using drug treatment than to use source-country interventions, interdiction, or drug law enforcement. The committee agrees that drug treatment should not be evaluated according to a standard of perfect abstinence, but rather by its ratio of benefits to costs, and its cost-effectiveness relative to other interventions. Unfortunately, the CALDATA benefit-cost ratio and the RAND cost-effectiveness estimates are based on problematic estimates of treatment effectiveness drawn from uncontrolled observational studies. At present, there is little firm basis for estimating the benefit-cost ratio or relative cost-effectiveness of drug treatment.
We begin by articulating a philosophy of constant treatment improvement through the use of successive randomized controlled clinical trials. We then offer several illustrative examples of compelling experimental research programs. We note the inferential limitations of controlled trials that lack a no-treatment control group. We describe potential opportunities for supplementing existing treatment versus treatment trials with treatment versus no-treatment experiments. We then examine one such domain of opportunity—treatment as an alternative or adjunct to criminal justice sanctions. Finally, we note the potential loss of clinical utility in
highly constrained randomized trials and describe analytic methodologies for the more powerful use of nonexperimental observational studies of drug treatment in realistic (and often difficult to study) clinical settings.
CONSTANT IMPROVEMENT OF TREATMENT EFFECTIVENESS VIA A PROGRESSION OF RANDOMIZED TRIALS
In modern medicine, treatments intended to benefit human subjects are evaluated in randomized controlled trials (Peto et al. 1977a, 1977b; Freidman et al., 1985; Meinert, 1986; Piantadosi, 1997; Pocock, 1996). Typically, a new treatment innovation that aims to improve outcomes is compared with an effective, current standard treatment by assigning subjects at random, using random numbers, to either the new treatment or the standard treatment. Random assignment ensures that comparable patients receive competing treatments. The current standard treatment may, in some instances, be no treatment at all, as may occur if no treatment is known to be effective, and if patients are willing to be randomly assigned to no treatment. (The latter condition is often a major obstacle to successful randomization.) A sequence of randomized trials increases the likelihood and rapidity with which improved treatments will replace less effective treatments.
Perhaps the most famous and most instructive example of a randomized trial involves prevention rather than treatment. It is the 1954 trial of the Salk vaccine for poliomyelitis (Meier, 1978). More than 400,000 children were randomly assigned to either the vaccine or a placebo. In the randomized trial, the rate of polio was more than 2.5 times higher in the placebo group than in the vaccine group (Meier, 1978: Table 1), and this finding quickly led to the widespread adoption of the vaccine. Randomized trials quickly create scientific consensus, and often scientific consensus is needed if scientific evidence is to affect public policy.
The Salk trial is instructive not only because of its enormous size and immediate impact on public policy and public health, but also for methodological reasons. Some states refused to participate in the randomized trial. Instead, these states compared vaccinated 2nd graders to 2nd graders who were not vaccinated and to 1st and 3rd graders who were not offered the vaccine. These comparisons were less satisfactory than the comparisons in the randomized trials, for three reasons. First, random assignment of treatments provides a tangible reason to believe the difference in outcomes in vaccinated and placebo groups was caused by the vaccine (Fisher, 1935). Second, in the states that refused to randomize, the vaccine appeared less effective, with unvaccinated second graders having rates of polio only 1.76 times higher than vaccinated 2nd graders, and 1st and 3rd graders having rates of polio only 2.16 higher than vaccinated
2nd graders (Meier, 1978: Table 1). Third, in the states that refused to randomize, the two possible control groups did not agree with each other: the 1st and 3rd graders had a 20 percent higher risk of polio than unvaccinated 2nd graders. In the states that refused to randomize the effects of the vaccine were more ambiguous in principle, smaller in apparent size, and internally inconsistent.
Before randomized trials became the norm in medicine, costly innovations were regularly introduced into standard medical practice, only to discover, years later, that the innovations were ineffective or harmful (Barnes, 1977). The Salk vaccine trial is typical, not atypical: carefully controlled studies often reach different conclusions from poorly controlled studies, and the carefully controlled studies, even if few in number, have the greatest impact on scientific consensus (Chalmers et al., 1972, 1983).
There is considerable debate about the ethics of randomized trials, but certain principles are widely endorsed; see Piantadosi (1997: Chapter 3) for a survey of this literature. Randomized trials are typically ethical when there is no clearly effective treatment, or when there is genuine and realistic uncertainty, reflected in a lack of scientific consensus and limited evidence, as to which of two treatments confers greater benefits with fewer harms. Randomized trials are typically ethical when haphazard circumstances might, in the normal course of events, assign patients to either of two treatments, both of which are realistically hoped to be beneficial. Randomized trials are typically ethical when a new treatment holds realistic promise of substantially improved outcomes but is as yet unproven, and so it cannot be made widely available outside experiments. Medical “practice based on unproven treatments is not ethical” (Piantadosi, 1997:33).
RECENT EXAMPLES OF STRONG TREATMENT EVALUATIONS
There have been a number of randomized controlled trials of treatments for opiate dependence (e.g., Woody et al., 1987) and cocaine dependence (e.g., Silverman et al., 1996; Crits-Christoph et al., 1999). In this section, we briefly summarize five recent treatment evaluation studies that, in the committee’s view, exemplify the methodological state of the art in drug treatment research. This selection is intended to be illustrative, not exhaustive. We do not assert that the conclusions of these studies are beyond reproach; indeed, in a later section, we discuss inferential shortcomings of these studies and methodological steps that might address them.
The highlighted studies are randomized trials, and they demonstrate that such experiments are possible in this field. They are noteworthy for the attention the investigators devoted to random treatment assignment,
treatment fidelity, measurement reliability and validity, and the use of research design and statistical analysis in an attempt to rule out possible alternative explanations. With respect to measurement, each study utilized continuous measures of success rather than a crude categorical “abstinent or not abstinent” outcome classification. To use abstinence as the only goal would be as erroneous as using complete absence of pain as the only goal of an arthritis treatment. In the real-world situation, the goal should be improvement.
G.E.Woody, A.T.McLellan, L.Luborsky, and C.P.O’Brien (1987) Twelve-month follow-up of psychotherapy for opiate dependence. American Journal of Psychiatry 144:590–596.2 A total of 120 male veterans who were addicted to opiates were randomly assigned to one of three treatments while maintained on a level dose of methadone: (a) paraprofessional drug counseling only, (b) counseling plus professional supportive-expressive psychotherapy, or (c) counseling plus professional cognitive behavioral psychotherapy. They were evaluated at a 12-month follow-up using a battery of assessment instruments, including the Addiction Severity Index and several psychiatric diagnostic instruments. Though all three groups showed improvement at follow-up, the two groups receiving professional psychotherapy showed greater improvement by various criteria.
G.E.Woody, A.T.McLellan, L.Luborsky, and C.P.O’Brien (1995) Psychotherapy in community methadone programs: A validation study. American Journal of Psychiatry 152:1302–1308. This study conceptually replicated the research team’s previous counseling only versus counseling plus supportive-expressive comparison in three community-based methadone programs. This study also addressed a confounding factor in the original design—specifically, that the psychotherapy groups received attention from two therapists while the counseling only group received the attention of only one therapist. In this second study, data at a 6-month follow-up showed significantly better improvement in the supportive-expressive psychotherapy condition than in the counseling-only condition.
P.Crits-Christoph, L.Siqueland, J.Blaine, A.Frank et al. (1999) Psychosocial treatments for cocaine dependence. Archives of General Psychiatry 56:493. A total of 487 cocaine-dependent patients were randomly assigned to one of four treatment conditions. All groups received
Charles O’Brien is both a committee member and a coauthor of two of these studies. Note that these particular studies were selected for inclusion in this discussion by consensus of the committee.
group drug counseling. In addition, one arm received individual drug counseling, one received cognitive therapy, and one received supportive expressive therapy. Outcomes were measured using the Addiction Severity Index, a drug use score, and the number of days of cocaine use in the past month. Outcomes were assessed monthly during treatment period, and at 9, 12, 15, and 18 months after randomization. The best results were found for the group drug counseling+individual drug counseling group. The study and its presentation are noteworthy for the attention paid to protocol violations, with follow-up of violators, analyses of missing data and treatment integrity, assessment of possible unique therapist effects, and so on.
S.T.Higgins et al. (1995) Outpatient behavioral treatment for cocaine dependence: One-year outcome. Experimental and Clinical Psy chopharmacology 3:205–212. This study analyzes 12-month follow-up data from two randomized controlled trials, involving a total of 78 community residents who met DSM-III-R criteria for cocaine dependence. Both trials compared traditional drug abuse counseling to a community reinforcement approach involving spouses, friends, or relatives and employment and other counseling services, and an incentive voucher system in which participants earned retail vouchers of modest monetary value for each negative urinalysis over a 24-week period. The first trial compared traditional counseling and the community reinforcement approach+vouchers; the second compared the community reinforcement approach alone to community reinforcement approach+vouchers. Outcomes included the Addiction Severity Index and urine test results. All conditions showed significant improvement over the course of the trials; community reinforcement approach+vouchers was superior to traditional counseling on various outcome measures, but the community reinforcement approach alone and community reinforcement approach+vouchers did not significantly differ from each other. The authors acknowledge that the small sample size provided adequate statistical power for within-treatment effects but inadequate power for post-treatment follow-up results.
K.Silverman, S.T.Higgins, R.K.Brooner, I.D.Montoya, E.J. Cone, C.R.Schuster, and K.L.Preston (1996) Sustained cocaine abstinence in methadone maintenance patients through voucher-based reinforcement therapy. Archives of General Psychiatry 53:409–415. This study usefully complements the Higgins et al. study cited above, extending that research in two ways. First, this study examined the effects of a similar voucher-based treatment for cocaine use, but among heroin abusers in a methadone maintenance program rather than community volunteers. Second, this study compared the contingent voucher program to a control condition in which participants were yoked to members of the treatment group; these latter participants thus received vouchers that were not con-
tingent on their own drug use patterns. Those in the contingent voucher condition showed greater reductions in cocaine use than those in the noncontingent vouchers; importantly, the noncontingent vouchers significantly reduced attrition from the study. Thus, it appears that vouchers reduce dropout rates, but that contingent vouchers promote reductions in use that are not solely attributable to remaining in treatment. This study shares a weakness of the Higgins et al. study—a small sample size that limits the statistical power of the analyses.
It is useful to contrast these studies with some of the major American treatment outcome research initiatives of the past 30 years:
The Drug Abuse Reporting Program (DARP—see Simpson and Sells, 1982, 1990),
The Treatment Outcome Prospective Study (TOPS—see Hubbard et al., 1989), and
The Drug Abuse Treatment Outcome Study (DATOS—see Simpson and Curry, 1997).
DARP, TOPS, and DATOS were three large-scale, multisite, multi-investigator initiatives involving tens of thousands of clients, hundreds of clinicians, and a broad range of treatment modalities and therapeutic techniques, client characteristics, and drug abuse patterns. These were ambitious efforts that addressed multiple goals. One goal was descriptive—to attempt to describe the universe of treatment clients, settings, and modalities in the United States. Another goal was inferential—to assess the effects of drug treatment on various client outcomes. Arguably, programs like the Treatment Episodes Data Set (TEDS) and the National Drug and Alcohol Treatment Unit Survey (NDATUS) are better suited for the routine collection of aggregate descriptive statistics about trends in national delivery of drug treatment services. For the second, inferential goal, in the committee’s judgment, future research funds would be better spent on a large number of randomized clinical trials, with cross-site extensions and replications. Because they lacked randomized assignment to condition, DARP, TOPS, and DATOS could not provide rigorous evidence on the relative effectiveness or efficacy of particular drug-by-treatment combinations, or for estimating the absolute effect size, cost-effectiveness, or benefit-cost ratio of treatment. The committee recommends that priorities for the funding of treatment evaluation research should be changed; large-scale, national treatment inventory studies should not be conducted at the expense of greater funding for randomized controlled clinical trials.
ELIMINATING INFERENTIAL ARTIFACTS AND ESTIMATING ABSOLUTE EFFECT SIZES
Considering the enormous challenges of conducting research in clinical settings, the randomized trials highlighted in the previous section are quite rigorous. They are a powerful source of information for improving drug treatment. But as designed they cannot provide robust estimates of the absolute magnitude and range of treatment effects for various types of clients (especially voluntary versus coerced clients), which are needed for use in cost-effectiveness comparisons, benefit-cost analyses, and simulation modeling of the potential benefits of scaling up or expanding the current treatment system.
The inferential benefits of randomization to experimental condition are well known; see Cook and Campbell (1979) for a comprehensive listing of threats to validity that are reduced or eliminated by randomization. (Note that design limitations create vulnerability to biased inference; they do not guarantee that biased inferences will occur. Whether any bias actually resulted is an empirical question.)
Here, we emphasize the various processes that can differentially bias selection into, or attrition out of, the treatment and control conditions of the study. When other factors are confounded with the treatment variations under study—e.g., addiction severity, motivation to change, life stresses and resources—it is not possible to directly estimate treatment effects by simply examining the difference between mean outcomes in each condition.
Many of these selection biases result from the causal forces that bring clients into treatment. The net directional effect of such biasing processes is rarely clear. Consider a nonexperimental study in which treatment clients are compared with a demographically matched sample of drug users not in treatment. On one hand, one might expect that those who seek and stick with treatment might be more motivated to give up their drug use (see DiClemente, 1999). On the other hand, many if not most clients are in drug treatment not because they voluntarily chose to be, but because they were either formally or informally coerced by a court, law enforcement agency, employer, spouse, or family member. For example, in the 1997 TEDS study, 34.9 percent of all admissions were referred by the criminal justice system (Substance Abuse and Mental Health Services Administration, 1999: Table 3.4). (We briefly examine the literature on coerced treatment below.)
Moreover, at least in the case of tobacco smoking, there is some evidence that smoking cessation clinics disproportionately see the hardest cases—those who were unable to quit smoking on their own (Schachter, 1982). Some selection biases involve client or setting characteristics that
are confounded with assignment to or completion of treatment. Others involve dynamic processes of change that are unrelated to treatment, such as external influences that affect drug use (e.g., changes in prices, changes in employment or marital status; see Campbell and Stanley’s (1963) discussion of “history” artifacts), autonomous internal processes of change in the individual (what Campbell and Stanley call “maturation” effects), or the statistical effects of random variation in client outcomes over time (regression to the mean).
Regression to the mean is a purely statistical phenomenon that can mask a causal relationship between variables. When the association between an independent variable and a dependent variable (or between measures of a variable at two different points in time) is imperfect, objects or people with extreme scores on the first variable will often be less extreme on the second variable, and vice versa. Hence, predictions from one variable to the other are “regressive.” Treatment studies are particularly vulnerable to regression artifacts if clients are most likely to seek treatment when their drug use or related problems become extreme. As Higgins (1999:516) argues: “caution is imperative in interpreting pre- to post-treatment changes. Patients likely enter treatment when drug use and related adverse consequences have reached an uncomfortable intensity (for them and others), and thus the intake interview is likely to represent an extreme estimate. If so, subsequent assessments on average will be less extreme even in the absence of treatment due to the ubiquitous phenomenon of regression to the mean.”
Thus, even if treatment had no beneficial effect on clients, one might expect to see the same qualitative decline in drug use reported in most nonexperimental pretreatment/posttreatment comparisons—a chance fluctuation in drug use and problem frequency, followed by a noncausal return to average levels. Note that regression to the mean provides one plausible interpretation—but certainly not the only interpretation—of the widespread belief that alcoholics and other addicts need to hit rock bottom before they will be ready to change their behavior (but see McLellan et al., 1992, for evidence that a small sample of patients on a waiting list reported worsening rather than improving symptoms over time).
Because these various biases can occur in either an upward or downward direction, their net effect on treatment outcome estimates is unclear. Note that the treatment estimate from a single study may reflect biases in both directions, and the relative effect of each bias may differ across studies. Randomized clinical trials of the type illustrated in the previous section go a long way toward eliminating concerns about the biasing effects of regression to the mean, biased selection to treatment, and biased attrition. Indeed, such trials greatly reduce biases in estimates of the advantages of one treatment method over another one.
But these trials cannot rule out the possibility of constant biases— selection biases that affect each condition under study. Constant bias does not threaten inferences about relative effectiveness of one treatment over another across randomized conditions. But it does threaten inferences about the absolute size of any treatment effect, relative to zero, making cost-effectiveness or benefit-cost estimation hazardous. Moreover, constant biases make it difficult to accurately forecast the likely effects of expanding treatment coverage to include those not currently receiving services. To some extent, these inferential threats can be addressed through sophisticated statistical methods (discussed in a later section). But ultimately, the most persuasive strategy for addressing these concerns is the use of randomized trials with a no-treatment control group. According to Higgins (1999:517):
However, even in [recent] controlled trials, the absence of “placebo” or no-treatment control groups precludes precise estimates of what proportion of pre- to post-treatment changes are attributable to treatment. The cocaine-dependence treatment field would be well served by careful consideration of what additional experimental or quasi-experimental control conditions might be ethically and practically possible in future efficacy and effectiveness studies to help strengthen the validity of causal inferences and permit more precise estimates of the contribution of treatment to any changes observed.
The almost complete lack of no-treatment control groups in drug treatment research is striking. While there are numerous studies of placebo versus a new medication plus minimal counseling, studies of patients randomized to nothing at all are lacking. The drug treatment community has not ignored this issue (e.g., Anglin and Hser, 1990) but has generally responded with three plausible objections: clients are unlikely to agree to possible assignment to a no-treatment control group, no-treatment control groups are unethical, and there are alternative methods for achieving the same inferences.
Will clients agree to randomization to a no-treatment control group? The committee agrees that this is an important practical concern, but in the absence of such trials for drug treatment, it is not possible to estimate the magnitude of the problem. Presumably, this is a greater concern for studies of clients voluntarily seeking treatment than for studies of legally coerced clients (discussed below).
Are no-treatment control groups unethical? In brief, many clinicians argue that it is unethical to withhold treatment from those in need of it. Of course, one might counter that this begs the question of whether in fact drug treatment is beneficial. There is a competing ethical concern—the missed opportunities involved in failing to discover a more effective treatment because of undue faith in current standards of best practice.
The prevailing standard for judging the ethics of withholding treatment is called the equipose principle (Freedman, 1987, 1990). According to Freedman’s original (1987:144) statement of the equipose principle, it is ethically acceptable to withhold treatment if “there is no consensus within the expert clinical community about the comparative merits of the alternatives to be tested” (1987:144). Although it is clear that the drug treatment community lacks consensus on which therapeutic techniques and modalities are most appropriate for cocaine or marijuana dependence, it seems unlikely that treatment experts would question whether treatment is preferable to no treatment. The politics of funding—especially the appearance of a zero-sum budget battle among the various demand- and supply-side programs—creates pressures against actively questioning the effectiveness of one’s own interventions. And the history of science shows clearly that expert scientific communities often reach consensus in favor of invalid conclusions (see MacCoun, 1998 for a discussion of the effects of homogeneous bias in research communities).
There are numerous cautionary tales of premature medical consensus reached in the absence of clinical trials. Cohen (1998) cites three examples: the administration of oxygen to premature newborns, the Vineburg procedure for coronary insufficiency (sham cardiac surgery), and superficial temporal to middle cerebral artery anastomosis (the surgical connecting of 2 arteries). Similarly, recent large-scale clinical trials have cast doubt on conventional assumptions about the links between estrogen and female heart attack risk, and between dietary fiber and colon cancer.
These objections are largely addressed by Freedman’s subsequent refinement, the clinical equipose principle (1990), which contends that placebo controls are justified when (a) there is no standard treatment, or (b) the standard treatment is no better than a placebo, or (c) the standard treatment is a placebo, or (d) new evidence challenges the net effectiveness of the standard treatment, or (e) an effective treatment is too scarce or too expensive to provide to every patient in need. Regardless of one’s views about whether the first four conditions are met for cocaine treatment, it seems clear that the last condition is applicable.
Are no-treatment control groups unnecessary? A second objection to no-treatment control groups is the contention that other sources of evidence render them unnecessary. One might look toward observational data from so-called natural experiments involving the sudden cessation of treatment due to exogenous factors. For example, Anglin and Hser (1990) review evidence on the effects of two methadone clinic closings—a Bakers-field methadone maintenance clinic that was closed by local officials for budgetary and political reasons, and the discharge of clients from the California civil commitment program due to “relatively random legal errors.” They argue that in both cases, clients who abruptly ceased treat-
ment fared more poorly than those who received a full course of treatment. Such situations are not conclusive, but they do seem more informative than passive correlational studies that lack such exogenous shocks. Situations in which data collection is ongoing when such shocks occur are rare; we know of no examples involving cocaine treatment or modalities for heroin other than methadone maintenance.
Another line of relevant evidence comes from statistical comparisons of voluntary versus coerced treatment clients. The current consensus is that it does not matter—coerced clients fare no worse (and no better) than voluntary clients (see reviews by Anglin and Hser, 1990; Farabee et al., 1998; Lawental et al., 1996; Silverstein, 1997). Gostin (1991) argues that “the intuition that compulsory treatment will fail because drug dependent people must be self-motivated to benefit…simply is not borne out by the data.” For example, Silverstein (1997) found no significance outcome differences for court-mandated versus other clients at a semirural drug abuse treatment clinic. Lawental et al. (1996) found comparable improvements for both self-referred and employer-coerced private treatment clients.
These studies help to address concerns about regression and selection artifacts. However, these studies use quasi-experimental, “nonequivalent control group” designs, comparing coerced and noncoerced clients at the same site. Although most of these studies attempted statistical matching, there is no way of knowing whether the coerced and noncoerced groups are otherwise comparable; for all we know, the coerced clients could be individuals who would have benefited even more from treatment in the absence of coercion.
Finally, one could argue for the effectiveness of drug treatment by analogy to other behavior change interventions that have been more rigorously assessed. Other forms of psychotherapy have fared well under randomized, no-treatment control experiments. As discussed in Chapter 7, Lipsey and Wilson (1993) provided a comprehensive review of these literatures, and an enormously ambitious “meta-meta-analysis” of 302 published meta-analyses of treatment interventions. These meta-analyses did not include cocaine or opiate treatment, but they did include arguably similar interventions such as cognitive therapy for depression, tobacco cessation, and weight control. Across the 302 meta-analyses, they reported an average effect size of behavior change interventions of about half a standard deviation; 90 percent were greater than or equal to 0.10, and 85 percent were greater than or equal to 0.20. For smoking cessation, the effect sizes ranged from 0.21 to 0.62 in magnitude; all were reliably above zero. But none of these interventions is perfectly analogous to treatment for psychoactive drug dependence. There are undoubtedly differences across domains in client characteristics, etiology, mechanisms of pathol-
ogy, legal status, and social stigma that preclude confident generalization to the drug domain.
Moreover, these studies only evaluated the self-selected group of patients who presented for treatment rather than the universe of sufferers in the community. For drug addiction, we would like to know the effects of treatment on all of those with the disorder, including those not presenting for treatment. Because the number of current treatment slots can only accommodate a fraction of those with the disorder, a critical policy question is whether the creation of additional slots is cost-effective. Finding the answer would require a control in the community randomized to no treatment whatsoever.
The meta-analytic data do suggest that nonrandomized trials don’t invariably inflate effect sizes. Lipsey and Wilson (1993) found no reliable differences in the effect sizes between experiments (mean=0.46) and quasi-experiments (mean=0.41). Shadish and his colleagues (Heinsman and Shadish, 1996; Shadish and Ragsdale, 1996), in more rigorous meta-analyses of data from a sample of the domains covered by Lipsey and Wilson, found that effect sizes tended to be significantly larger in randomized experiments, even after controlling for various confounding differences between experimental and quasi-experimental studies.
In this regard, a study by McKay et al. (1998) is relevant. These authors compared patients either randomly assigned to cocaine treatment and those who “self-selected” into the same treatment settings, finding “greater problem severity at intake among randomized patients coupled with greater improvements by 3-month follow-up relative to the nonrandomized patients” (McKay, 1998:697). The investigators argue that “randomized studies of treatment for cocaine abuse may produce somewhat larger estimates of improvement than what is observed in more typical treatment situations” (see Campbell and Boruch, 1975, for a relevant discussion).
Thus, it is our contention that randomized experiments with no-treatment controls provide more accurate estimates of the efficacy of drug treatment, not necessarily smaller estimates. We do not contend that such no-treatment controls are essential for testing possible improvements in treatment methods; randomized “Treatment A versus Treatment B” trials are a powerful mechanism for that goal. Rather, in the committee’s view, no-treatment control groups are necessary to provide the kind of information needed to support policy analyses of the effectiveness and cost-effectiveness of providing drug treatment and of expanding treatment access.
Bias due to incomplete compliance with randomized assignment. In some settings, the experimenter can encourage compliance with the treatment protocol, but some experimental subjects may not comply. Realistically, some proportion of clients in a no-treatment control group may seek out
treatment outside the clinical trial; similarly, some fraction of treatment group may fail to attend treatment sessions. Statistically, this noncompliance adds “noise” to the design, and possibly a bias to the estimated treatment effect size. Random assignment of treatments is nonetheless of great value, even though compliance may be imperfect. Recent developments in analytical methodology simultaneously use both the random assignment of intended treatment and the treatment actually received. See Angrist et al. (1996), Balke and Pearl (1997), Manski (1990, 1995), Robins (1989), Rosenbaum (1996, 1999a), Sheiner and Rubin (1995), and Sommer and Zeger (1991) for various approaches.
OPPORTUNITIES FOR RANDOMIZATION WITH NO-TREATMENT CONTROL CONDITIONS
When a pharmaceutical manufacturer makes claims about the efficacy or effectiveness of a new drug product, the U.S. Food and Drug Administration advisory committees looks to the evidence from randomized controlled trials in which eligible participants have been assigned at random to different conditions (e.g., new drug regimen versus usual and customary regimen, new drug regimen versus placebo regimen). In this context, over the long run, randomization is supposed to bring into balance all of the influences on the effects of interest, but for the randomly assigned intervention status. In consequence, randomized designs can provide an especially illuminating body of evidence about the efficacy and effectiveness of newly proposed interventions. It is when the new treatment regiment is compared with a no-treatment control condition that we can gain the most complete evidence of intervention impact. Of course, “no treatment” is rarely an absolute. In reality, new medications are compared against placebo treatment while both placebo and new medication groups receive standard evaluation and non-specific care.
Despite the broadly acknowledged superiority of evidence from randomized designs with no-treatment controls when the task is to assess treatment effects, some observers feel strongly that the benefits of randomization are overstated in studies about the effects of promising therapeutic or preventive interventions (see the next section). These observers argue that randomized trials create impediments to generalizable results of immediate public health significance. In addition, when individuals are seeking treatment for their drug problems, there might be ethical or logistical barriers to the no-treatment control condition that is required to gauge an intervention’s effects completely.
It is beyond the scope of this report to settle this issue. However, we do consider some possible situations in which it would be ethical and just to make a random assignment of different interventions, including the
no-treatment control condition, in order to gain a more complete, accurate, and precise estimate of the intervention’s impact on treatment or prevention of drug problems.
Within the domain of drug intervention research, there may be some missed opportunities for randomized clinical trials, with no-treatment control conditions, that could otherwise be used to assess the efficacy and effectiveness of new treatments or preventive interventions. In this section, we describe several opportunities for research of this type.
In general, the committee has looked into possibilities for placebocontrolled randomized trials that are not being exploited as completely as they otherwise might be. In this context, the first missed opportunity involves the workers (generally unskilled) who now are required by public or private employers to undergo randomly administered drug tests. Many of these workers undergo the tests during an initial review period during which a resume or application has been filed and thereafter periodically during follow-up assessments. Most often, when the workers show a test result that indicates recent drug use, they have not been hired or retained in the job for which they have applied, or they are suspended from their jobs, often without employee assistance or interventions to address underlying drug dependence or other condition that fostered the positive drug test result.
Situations of this type, especially those of preemployment drug testing, represent some missed opportunities for randomized controlled trials to compare drug dependence intervention strategies with no-treatment alternatives. The no-treatment alternative meets most ethical standards because current practice is to provide no treatment to these individuals, but simply to advise them that they have lost the privilege to be hired into the job for which they have applied. In addition, it seems that few of these individuals go out and seek treatment once they have received a positive test result. In situations of this type, an investigator could recruit the prospective employees who have just failed their drug tests, and use randomized designs to test new intervention strategies against the no-treatment alternative. Such patients would have to be evaluated prior to randomization in order to segregate them according to occasional use, abuse, and dependence, since previous studies have found that most of those detected in preemployment drug testing do not meet criteria for dependence.
A second set of opportunities involves health maintenance organizations and managed care practices with health benefits that do not include drug treatment. In these situations, subscribers in need of drug treatment can be offered the chance to enroll in a randomized trial, with a result that some large randomly chosen fraction of those needing treatment receive care subsidized by the health organization, whereas the remainder re-
ceive usual and customary care within that practice (namely, no treatment). Here, again, ethical concerns about the research are addressed because at least some individuals will receive subsidized treatment, in a situation in which no one is receiving subsidized treatment.
Another set of opportunities for randomized trials with no-treatment intervention conditions is created by long-standing school policies to expel or suspend students who are found to be drug users. Here again, it is typical to separate the drug-using youth from the rest of the student body, at least for a time. However, it is not standard to provide treatment interventions for the drug dependence that may be prompting continued drug use despite the socially maladaptive consequences of drug use. As such, expelled or suspended students who volunteer to participate in a randomized trial could be randomly assigned to a treatment versus no-treatment condition, allowing estimation of treatment effects against a background of the usual and customary condition of no treatment.
Finally, despite recently advanced federal Office for Protection from Research Risks (OPRR) restrictions on research with prisoners and probationers, the situations of drug-dependent individuals in prison or on probation can sometimes offer an opportunity for randomized trials with no treatment conditions. These situations arise when the prison or probation program is offering no treatment as the usual and customary condition for drug-taking individuals in their custody. In this context, random assignment to a drug treatment condition represents a potentially beneficial departure from the usual and customary condition of no treatment. As such, an array of randomization designs become possible (see further discussion below).
In summary, it often is difficult to argue in favor of randomization designs with no-treatment control conditions when the study participants are being drawn from individuals who are seeking treatment at drug clinics. We have outlined some of the missed opportunities for randomization designs with no-treatment conditions that are created because, at present, many drug users are identified without any formal treatment response.
The committee recommends greater scientific attention to now-missed opportunities to conduct randomized trials of drug treatments with no-treatment control conditions. Certainly, there will be obstacles not mentioned in this chapter. And there are other ethical and legal considerations that must be addressed in the design of such trials, such as protecting the confidentiality of the treatment records and insulating research records from legal or private uses. Nonetheless, the value of evidence based on randomized designs with no-treatment control conditions is sufficiently great to warrant considerable expenditure of effort to overcome these obstacles.
OPPORTUNITIES FOR RANDOM ASSIGNMENT IN THE CRIMINAL JUSTICE SYSTEM
Apprehension of drug users provides an opportunity to reduce drug use (and future offending) by using the threat of sanctions as a form of leverage to induce arrested or convicted users to participate successfully in treatment programs. In 1973, the National Commission on Marihuana and Drug Abuse concluded that the primary utility of criminal sanctions for consumption-related drug offenses lies in providing therapeutic leverage. During the past three decades, programs linking treatment and the criminal process have been developed and implemented with varying degrees of intensity across the country.
Not all treatment in the criminal justice system is coercive: treatment can be offered on a completely voluntary basis, without any connection to the offender’s charges or sentence. Many prison-based programs are of this type. (Conversely, it should be noted, treatment is sometimes compelled without any connection to the criminal justice system, as under a civil commitment statute.) In fact, however, most treatment provided to drug offenders is leveraged, in the sense that it is linked to case outcome or sentence severity.
In thinking about linkages between drug treatment and criminal sanctions, it is important to distinguish between questions of effectiveness and fairness. Supporters of using the criminal justice system for therapeutic leverage typically view treatment participation offered to offenders as an ameliorative device—an opportunity for mitigating the sentence that they would otherwise receive (i.e., probation with treatment is offered in lieu of incarceration, using the threat of incarceration for noncompliance). Others worry that programs of mandated treatment will actually have the effect of increasing the severity of punishment compared with what the offenders would otherwise have received (Covington, Appendix E). As an example, offenders who otherwise would have been sentenced to traditional probation could be subject to treatment conditions that create a risk of imprisonment (for noncompliance) that otherwise would not have existed. Or an offender whose case might otherwise have been dismissed could be sentenced to conditional probation. These are classic “net-widening” concerns, because they widen the reach and deepen the intensity of punishment. This issue should be kept in mind in considering research on coerced treatment.
Legal strategies to coerce drug users into treatment have been used both at the “front end” in diversionary programs and at the “back end” among parole and probation populations. However, experimental designs are rare, and it is difficult to disentangle the effects of treatment from the effects of coercion. Also, many studies have been concerned
primarily with treatment retention or length of stay, rather than treatment outcome or posttreatment involvement in drug use or criminal behavior.
A number of studies of prison-based programs seem to demonstrate positive postrelease outcomes, including reductions in drug use and crime along with improvements in employment, when inmates who have gone through prison treatment programs are compared with those who have not (Wexler, 1994; Wexler et al., 1999; Inciardi et al., 1997). However, research conducted to date has not yet convincingly demonstrated the effectiveness of prison treatment programs. Even in studies that find a significant relationship between completion of the treatment program and post-release outcomes, the overall positive effect is attenuated by inconsistent findings (e.g., outcomes were not related to dose of treatment, and the no-treatment control group delayed rearrest longer than the treatment groups). Moreover, positive treatment outcomes may be attributable to selection bias (e.g., the high level of commitment of offenders who complete the program rather than the capacity of the program to change their behavior). Also, since most research on effectiveness of prison drug treatment was done on older heroin addicts, the results may not be applicable to younger heroin addicts or to crack cocaine users.
Research on treatment of prisoners incarcerated in the late 1980s and the 1990s is confounded by the influx of tens of thousands of inmates whose drug use has been much less severe than that of earlier generations of prisoners. Positive posttreatment outcomes for these offenders may have less to do with the treatment than with their pretreatment conditions.
Treatment of Probationers
Most people convicted of drug offenses are not in prison. Thus, another key policy question is the effectiveness of using conditional criminal justice dispositions (e.g., pretrial diversion, probation, parole) to mandate drug treatment in the community. At least 60 percent of adults under criminal justice supervision are on probation. Yet the existing literature on probationary drug treatment fails to compare the effectiveness of linking probation to treatment conditions with other community-based criminal justice dispositions or with no intervention at all. The need for such comparisons—between those on probation and a no-supervision control group—becomes more relevant as the net is widened to include drug users who would not have been arrested or put on probation in previous years. The possibility exists that any seeming improvements in the suc-
cess rates of drug-using probationers over the years could be wrongly attributed to probation itself rather than to the inclusion of offenders with less severe drug and crime problems.
Treatment Alternatives for Street Crime
During the 1970s, the White House Special Action Office for Drug Abuse Prevention and the National Institute on Drug Abuse joined with the Department of Justice to link treatment with criminal justice through a variety of initiatives, the most important of which was Treatment Alternatives to Street Crime (TASC). TASC represents a structured postarrest diversion process under which successful compliance with treatment conditions results in dismissal of the charges without conviction. The effectiveness of TASC was examined using a subsample of subjects drawn from the TOPS study. Hubbard et al. (1988) found that TASC clients stayed in treatment longer and reported less posttreatment drug use than clients who had entered treatment without criminal justice pressure. However, pretreatment differences between the samples and differences in the services received make these findings difficult to interpret. Anglin et al. (1999) used random assignment at two of five study sites. One site showed no beneficial effects of TASC; the other showed reductions in some drug use measures but not on criminal recidivism.
The substantial increase in drug arrests and of drug-involved offenders in the late 1980s and 1990s stimulated innovative efforts to link the criminal justice system with community treatment programs. Building on the TASC model, hundreds of jurisdictions have established drug courts (usually specialized dockets rather than separate courts) to identify drug users in the criminal justice system, refer them to treatment programs and monitor their progress (Belenko, 1998, U.S. General Accounting Office, 1997). Since all of the drug court initiatives are relatively new, outcome data are limited, and their efficacy remains open to question.
The renascent interest in drug treatment/criminal justice linkages heightens the need for rigorous studies of the therapeutic utility (and cost-effectiveness) of these coercive legal strategies. To what extent, and under what circumstances, does coerced treatment through the criminal justice system achieve beneficial effects, compared with voluntary treatment, through nontherapeutic criminal justice intervention or with no intervention at all? Although more than 20 evaluations have been conducted, various factors make it difficult to draw definitive conclusions
(Belenko, 1998; U.S. General Accounting Office, 1997). First, there are enormous variations in eligibility requirements and program characteristics. Second, the U.S. General Accounting Office found that a majority of programs tended to assess recidivism and not relapse or, less frequently, relapse but not recidivism. Third, most of the existing studies are uncontrolled comparisons involving before-after or nonrandomized comparison groups, with the kind of threats to internal validity discussed earlier in this chapter. While many of these studies report reductions in drug use or criminal recidivism, it is notable that neither result clearly emerged in a rigorous study using random assignment to either drug courts or standard probation (Deschenes et al., 1995).
A Proposed Example
There is a clear need for more rigorous experiments on the effects of drug treatment as an alternative or adjunct to criminal justice sanctions. In the committee’s judgment, such experiments are logistically feasible and can be designed to be ethically defensible. Here we offer an example of a possible experiment by way of illustration.
A population of prisoners incarcerated for drug-related crimes could be randomized prior to release from prison. They would be segregated first by drug use category (heroin addicts, cocaine addicts, cocaine/alcohol, cocaine/heroin, etc.). The specific treatments for each category would differ. Subject characteristics to be assessed prior to release would include Addiction Severity Index scores, educational level, prior employment history, marital status, and other risk factors for drug relapse.
Within each category, one group of subjects would be randomized to follow-up as usual by the parole system with no contact with either treatment or research. Evaluation data at each visit would be obtained by a parole officer. Prisoners would be randomly assigned to one of three groups: (1) standard parole; (2) Treatment A; (3) Treatment B. A patient assigned to Treatment A could refuse treatment and receive standard parole instead, but this patient would remain part of the Treatment A group. Similar procedures would be followed for Treatment B. This is Marvin Zelen’s (1979) randomized consent design.
It is likely that some subjects assigned to standard parole will enter treatment on their own, and some other assigned to groups A or B will refuse treatment; this fact would have to be considered in the data analysis.
Similarly, the predictor variables obtained prior to randomization would have to be assessed, to determine the comparability of the four groups and for use as covariates in analysis of outcome data.
An advantage of this design is that no one would get less than the standard probation counseling, but only randomly selected subjects would receive treatment. A necessary limitation is that a self-selected group who had been randomized to treatment would refuse to participate, but since they are in the probation system, they could be followed anyway.
The criminal justice component of this design raises complex analytic, legal, and ethical issues above and beyond those in an ordinary treatment experiment. Based on the view that drug dependence is a chronic relapsing disorder, many experts believe that abstinence is inappropriate as a sole or primary evaluative criterion. Yet positive drug tests are typically used as a trigger for sanctioning in mandated treatment regimes. Thus a key concern, from both an ethical and a scientific standpoint—is whether either of the treatment regimes is more restrictive than the baseline parole regime. For example, would the parolees in all groups be subject to monitoring (e.g., drug testing) on the same terms? Would they be subject to revocation on the same terms? Variations on the proposed design might include intensity of monitoring as a treatment variation, or the use of graduated sanctions less severe than a return to prison (see Kleiman, 1997). Another question is whether program effects should be reported while the coercive leverage of parole supervision is still operative, or only after parole supervision has ended. This is both a methodological concern and a question of policy: To what extent is coercive leverage necessary (or even sufficient) for any observed treatment effect? These questions reflect the tensions inherent in a program that combines therapeutic and social control objectives. The relative restrictiveness and punitiveness of traditional vs. treatment-oriented sanctioning options is an important issue that merits careful attention.
The committee recommends that treatment researchers take greater advantage of possible opportunities for randomization to no-treatment control groups. For example, we strongly encourage studies of incarcerated and postincarcerated prisoners as outlined in this report. The committee urges federal and state agencies and private institutions to minimize organizational obstacles to such studies, within ethical and legal bounds.
TOWARD STRONGER OBSERVATIONAL STUDIES
The committee strongly recommends that treatments intended to benefit people be evaluated in carefully conducted randomized controlled experiments. At times, however, such experiments are not possible. For example, it is not possible to experiment with treatments be-
lieved to be harmful. For instance, it is important to know the effects on children of cocaine use by their mothers while pregnant, but this cannot be studied in an experiment. In observational or nonexperimental studies of treatment effects, the absence of random assignment of treatments may seriously bias comparisons of treated and control subjects. Many authors in the drug treatment literature recognize these concerns (e.g., Anglin and Hser, 1989), but in the committee’s judgment, many observers have too often relied on large observational studies instead of randomized trials to draw conclusions about the effectiveness of treatment.
A detailed discussion of methods for observational studies is not possible in this report. Good discussions of these methods may be found in Cook and Campbell (1979), Manski (1995), and Rosenbaum (1995). Although there is a great deal of agreement about methods for observational studies, there is some disagreement as well. Some of the disagreements are captured by the exchange between Rosenbaum (1999b), Manski (1999), Robins (1999), and Shadish and Cook (1999).
One common argument for nonrandomized studies is that the requirements of a randomized trial make it too artificial to describe treatment as it actually occurs in the field—the “effectiveness versus efficacy” debate. Meta-analyses by Shadish and colleagues (1997, 2000) do find that nonrandomized evaluations of psychotherapy are more clinically representative, but these meta-analyses do not indicate that clinical representativeness is associated with psychotherapy effect sizes.
It may be true that carefully controlled trials are less broadly representative than large-scale observational studies, but even the latter cannot guarantee generalizability across settings and over time. Medical researchers and social scientists alike are increasingly reluctant to rely on single studies, of any sort. There is a growing understanding of the need to look for converging patterns across experiments. In this light, the committee applauds the recent National Drug Addiction Treatment Clinical Trials Network of the National Institute on Drug Abuse that is now conducting large-scale randomized, controlled trials in average treatment programs in communities across the country. These studies should provide a more accurate picture of treatment effectiveness for the nation as a whole. But even in the absence of such an initiative, meta-analytic techniques make it possible to aggregate and compare data across studies (Cook et al., 1992). From a meta-analytic standpoint, heterogeneity across settings, populations, and experimental variations is advantageous for determining whether conclusions are robust, and whether there are important boundary conditions on a phenomenon. The identification of apparent cross-study moderating variables is often a valuable stimulus for theory development, suggesting important variables to test in subsequent experiments.
The committee recommends broader use of meta-analytic techniques for cumulating and comparing findings across treatment outcome studies.
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