Do school-based drug and alcohol prevention programs have any effect on subsequent use of these substances by students? Twenty years ago the answer would have been a resounding "no." Many programs were in fact found to have negative effects, leading a 1973 government report to recommend a moratorium on school-based drug prevention (+1). All this changed, however, in the mid-1980s with the "discovery" of the social influence approach that purported to teach children the skills necessary to resist social pressure to use drugs. Read almost any literature review in this area, and the story unfolds as follows.

In the 1960s and 1970s we relied on strategies—first giving factual information and then trying to make children feel good about themselves ("affective" education)—that research showed to be ineffective (+2,+3). In the mid-1980s, researchers began to develop and test programs that were based on sound psychological theories, such as social learning theory and problem behavior theory. Evaluations of these programs showed that they were successful in preventing a wide range of undesirable behaviors, including alcohol and drug use. Thus, unlike previous approaches that were not theoretically grounded or supported by empirical findings, the new approach had the distinction of being "science-based."

The trickle-down effect from the research world to the frontline practitioner was at best a dribble; there was little institutional diffusion of social influence programs during the early 1990s (+4). This state of affairs might have prevailed had illicit drug use not increased in the mid-1990s, leading politicians and others to question what we were getting for the money spent on prevention efforts. In response, federal agencies began to demand that recipients of funds use only programs that were supported by scientific evaluation research. As a result, almost every federal agency with responsibility for drug prevention has produced a "best practice" or "science-based" list of approved prevention programs during the past five years (+5,+6,+7).

Most of the school-based programs that appear on these best-practice lists are variants of the social influence approach. Unfortunately, it is difficult to use the term "best practice" to describe the evaluation research that is conducted in relation to many of these interventions. In fact, much of what goes on in the analysis of these school-based prevention programs is simply not consistent with the type of rigorous hypothesis testing that one associates with the term "science" and that has been a mainstay of evaluation research for the past 25 years (+8). I have described many of these practices—such as multiple subgroup analysis, post hoc sample refinement, and use of points in time other than the study baseline to calculate attrition rates—in a number of recent publications (+9,+10,+11,+12). In this column I briefly describe two other common practices, using as examples three of the most widely advocated prevention programs—the Seattle Social Development Project (SSDP), the Life Skills Training (LST) program, and the ATLAS program.

The adjustable outcome can take two forms, one more subtle than the other. In its most obvious form, the adjustable outcome involves a total change in outcome over the course of the evaluation. For example, the SSDP, developed by David Hawkins and colleagues at the University of Washington, has been promoted as a delinquency and drug use prevention program for the best part of 20 years (+13), but recent evaluations show that it has very little effect on such behaviors (+12,+14,+15). However, because these evaluations have produced some positive effects on some health-related sexual practices, such as condom use, among some of the intervention group, the SSDP is now being heralded as a sex prevention program (+15,+16).

In its more subtle form, the adjustable outcome involves a change in the way the variable is constructed from study to study rather than a total change in target outcomes. For example, a recent critique of a longitudinal evaluation of Gilbert Botvin's LST program (+17) observes that there was a shift from the use of continuous outcome measures—for example, a 9-point scale of marijuana use—in the initial report from the study (+18) to less sensitive dichotomous yes-or-no measures in a later paper published in JAMA (+19). This begs the question as to whether the results of the trial are measurement dependent. Specifically, would the positive program effects reported for a subsample of the study population in the JAMA paper have emerged from an analysis based on the continuous measures used in the initial report?

Moreover, when one looks across the entire body of LST evaluations, there are other similar instances in which the manner in which outcome variables are constructed changes from study to study, and even from report to report. For example, a 1992 study of the effects of the program on smoking among students from 47 New York City schools (+20) presented outcome data in terms of three dichotomous measures (use during the past month, the past week, and the current day) as well as an 11-point quantity scale, whereas a 2001 report from a study of students in 29 schools in the city (+21) used just two continuous scales (a 9-point frequency and an 11-point quantity scale). Furthermore, a 2003 report from the latter study presented smoking outcomes in terms of a composite measure that combined the mean score on the 9-point frequency scale with those on an 8-point quantity scale (+22). Again, one is left wondering whether the consistency in effects claimed for the program would exist had a consistent method been used in operationalizing the behavioral outcomes.

Although nothing is carved in stone about the level at which statistical significance is set, the traditional level is .05—that is, accepting a 5 percent probability that one's findings are due to chance. Using a p value of .1 obviously doubles the likelihood of finding a statistically significant effect, as does the use of one-tailed significance tests since the critical region is then shifted to one end of the distribution. Statisticians typically recommend that researchers limit use of one-tailed significance tests to situations in which there is a very strong prior hypothesis (+23). In the case of evaluations of prevention programs, their use would be limited to instances in which previous research led one to expect only positive, not negative, effects on outcomes in such situations.

The 1995 analysis of the LST program (+19) used one-tailed tests in examining effects on alcohol and marijuana use, even though a previous published evaluation of the program (+24) showed that it had virtually no effect on participants' marijuana use and actually had some negative effects on use of alcohol. Similarly, a recent evaluation of the ATLAS program (+25) used such tests in assessing the effects of the program on steroid use, even though an earlier report from the study (+26) indicated that the program had no effect on this behavioral outcome (+11). Thus there was no empirical basis for using one-tailed significance tests with the behavioral outcomes in either study.

When I raise such concerns about the evaluation practices employed in school-based prevention research at conferences or among colleagues, I frequently get three responses—none of which has too much to do with a science-based approach to prevention. The first response is usually along the lines of "Who are you to criticize these programs and the accompanying research when experts have declared them effective?" Such an attitude is decidedly antiscientific, because it fundamentally rejects a basic tenet of critical thinking—namely, that one judge a thought or idea on the basis of its content, not by the person of the thinker (+27).

The second response to my critique takes the form of "You shouldn't criticize these programs unless you have some alternative intervention to recommend." If the premise of this argument were accepted, then intervention studies would be subject to scrutiny only from those who have developed an alternative that has been shown to be effective; all others would be prohibited from commenting. Clearly, though, one's ability to assess the methodological soundness of an evaluation is in no way dependent on whether one has developed an alternative intervention program. Thus such an argument is entirely without any internal logic and hence is decidedly unscientific.

The final common response to my criticisms of evaluations of school-based prevention programs goes something like "Well, yes, we want prevention to be scientific, but the criteria you invoke are simply too strict. As a 'new science,' prevention should be able to bend the methodological rules a bit, especially in the interests of a good cause and with a program that we just know deep down must do some good." The problem with this argument is that these methodological rules and procedures have a purpose—namely, to isolate the effects of one's program from other influences that can bring about the type of behavioral change we desire—and when they are bent too much they no longer fulfill this purpose. Also, the rule bending tends not to be very evenly applied, and one is left wondering how prevention strategies that researchers have evaluated in the past and found to be ineffective—such as affective education and the Drug Abuse Resistance Education (DARE) program—would have fared had they been assessed with one-tailed significance tests, multiple subgroup analysis, and the like.

James L. Nolan, Jr., has observed that today's therapeutic state must balance its concerns about self-actualization and self-fulfillment with a utilitarian concern about effectiveness, efficiency, and cost. For the most part, the two coexist and even complement one another. However, when they come into conflict it is intuition and emotion that prevail over logic and reason (+28). Science-based school prevention programs are a prime example of this balancing act, and the response to critiques of evaluations of these programs demonstrates the triumph of the therapeutic perspective over the scientific.

This work was funded by a grant from the Smith Richardson Foundation, Inc.

Dr. Gorman is affiliated with the Department of Epidemiology and Biostatistics, School of Public Health, Texas A&M University System Health Science Center, 3000 Briarcrest Drive, Suite 310, Wells Fargo Building, Bryan, Texas 77802 (e-mail, gorman@srph.tamushsc.edu). Sally L. Satel, M.D., is editor of this column.