Translational Behavior Analysis and Practical Benefits

In his article, Critchfield (2011) summarizes a previous call (Mace & Critchfield, 2010) for basic scientists to reexamine the inspiration for their research and turn increasingly to translational approaches. Interestingly, rather than present an argument for the direct improvements to our science that might follow from a translational approach (a makeable case, though beyond the scope of the present commentary), Critchfield focuses instead on the social context in which our work takes place. He suggests that in a “world dominated by practical interests” (p. 6), investments in science are judged in terms of “practical benefits” (p. 4) and “social impact” (p. 3), and that translational research is necessary to “influence society's appreciation of basic science efforts” (p. 6). The call then is for a modified scientific agenda for basic researchers, with the modifications designed to enhance public relations.

Critchfield argues winningly that improved funding opportunities and better university support for faculty positions and laboratory infrastructure should follow if we conduct studies that “bear directly on” (p. 3), are “obviously relevant to” (p. 3), or “directly target” (p. 4) “problems about which laypersons and diverse scientific communities care deeply” (p. 3). These are critical outcomes, to be sure, and a thoughtful analysis of efforts that could lead to their attainment is much more than just an interesting intellectual exercise. Indeed, the very importance of these outcomes should mean that we take extra care to ensure that the analysis of controlling variables (over funding, hiring, etc.) is complete and not oversimplified. On the face of things, Critchfield's emphasis on the support to accrue from socially relevant research could seem self-evident. On closer consideration, however, it may be prudent to ask whether at least some of the assumptions on which this self-evidence rest are, if not unfounded, at least less than fully examined. To be clear, I am also a strong advocate of translational programs of study in behavior analysis and am thus in agreement with the basic premise of this article. The point at issue in this commentary involves the extent to which we can realistically expect translational programs of study for basic scientists, such as those espoused by Critchfield here, to positively affect public perception and thus, public support. As a corollary, we might consider whether an argument for translational research in terms of public relations will be the most effective route to producing change in basic behavior-analytic science.

To examine the aforementioned assumptions, let's begin with Critchfield's starting premise that “pure basic” science yields little in the way of “practical benefits,” and has thus fallen in stature in the eyes of society and in policy-level support. (It might be noted that despite taking Skinner to task for leaving the definition of interesting “open to investigator interpretation” [p. 5] in his infamous “Case History” suggestion, Critchfield says little about the criteria for defining practical benefits. Apparently it is enough to assume we would know a practical benefit if we saw one, although an argument could be made that benefits are often in the eye of the beholder.) Nevertheless, the implication is that translational research would yield, or would be more likely to yield, practical benefits. This critical point receives no attention, however. Critchfield asks appropriately enough about the proportion of basic science research programs that can be expected to yield practical benefits, but he sidesteps the equally appropriate question about the proportion of translational research programs that might be expected to yield practical benefits. If we are to increase basic behavior-analytic translational efforts based on society's demand for practical benefits, what evidence is there that such benefits would be forthcoming?

Alhough largely undefined by Critchfield, Mace and Critchfield (2010) outlined three categories of translational research programs that originate from basic behavior analysis. These include human replication of effects typically studied with nonhuman subjects (e.g., reinforcement schedule performances), laboratory models of naturalistic human phenomena (e.g., drug self-administration studies), and basic operant investigation of “uniquely human” behaviors (e.g., rule-governed behavior). Granted, Critchfield's argument is that these sorts of studies have been too few in number, but are their benefits to date supportive of translational research as a route to improved public appreciation? To be fair, we might even ask about the proportion of applied research studies that achieve the grail of practical benefits, especially if the emphasis is on practical (consider, e.g., the ongoing call for social validity assessments of work done in applied behavior analysis), and especially if the emphasis is on benefit beyond the participants in the study (i.e., having a social impact). Perhaps a disappointingly low proportion in answer to any of these questions speaks more to the necessarily cumulative nature of science than to inadequacies in the science itself. Very rarely does an individual experiment of any sort result in a practical breakthrough; in some sense then, most of the benefits of research are indirect. Perhaps our increased attention to high-quality science education for the broader public could facilitate greater appreciation of such indirect benefits, although this goal could take some time.

Further consideration is also warranted for the assumption that behavior-analytic translational (or even applied) research will necessarily have greater impact than “pure basic” science because it targets “problems about which laypersons and diverse scientific communities care deeply” (p. 3). Once again, we might question the support for this position, and Critchfield's message is sometimes confusing on this score. For example, the fate of discounting research is bemoaned here, although the basic behavior-analytic literature on the topic seems to include all three of the categories of translational research outlined by Mace and Critchfield (2010) (i.e., human replications; laboratory models; and naturalistic, if not exactly unique, human problems). Discounting has caught the attention of diverse scientific communities, including those that fund the research of behavior-analytic scientists, but its behavior-analytic inception is viewed as too indirect for translational purposes.

In a contrasting case, consider the example of research on stimulus equivalence, and relational stimulus control more broadly. This body of work has been implicitly and quite often explicitly translational since its inception almost 40 years ago (e.g., Sidman, 1971; Sidman & Cresson, 1973), situated squarely within the context of understanding language and verbal behavior, symbols, reference, and any number of “uniquely human” behaviors that result from facility with equivalence and other stimulus relations. Further, there exists a significant literature, also spanning 40 years, that describes effective applications of equivalence and related methods for populations ranging from children with severe developmental delays to college students, and targets ranging from simple reading, number, and money skills to university-level statistics and pharmacology content. Collectively, this work seems to exemplify perfectly the translational strategy prescribed by Critchfield; few laboratory models capture a comparable range of issues about which scientists and nonscientists alike care deeply. The question is whether societal and scientific interest has been commensurate with these efforts, or at least enhanced as a result of them, as predicted by Critchfield and others. In fact, few scientists outside behavior analysis have adopted equivalence or other relational training methods for research or for practice, and we would be hard pressed to document society's appreciation for them, despite clear demonstration of potential practical benefits.

It seems one could easily argue that behavior analysis (basic, translational, and applied) is replete with examples of direct benefits for socially important targets that have been largely ignored. A classic illustration is provided by Project Follow Through (e.g., Watkins, 1997), a national longitudinal study of the effectiveness of various teaching strategies for disadvantaged children, carried out over an 8-year period and involving approximately 10,000 children. Although direct instruction was the only one of 12 different teaching models to show educationally meaningful improvements over a nontreatment comparison group in each of three categories of outcome measures (basic skills, cognitive-conceptual skills, and self-concept), and although most of the other models showed significant negative effects (a second behavior analysis model showed improvements in two of the three categories), special federal commissions validated programs regardless of their impact on academic skills and disseminated them to school districts as equal options. What has this to do with translational research in basic behavior analysis? If evidence of clear benefits for a problem at the level of public education is insufficient to secure public attention and support, one might question the premise that human replication studies or laboratory models of interesting human phenomena are likely to do so. Indeed, it seems that factors in addition to direct benefit are of great consequence in the arena of public affairs and deserve their own analyses.

In his formula for translational research, Critchfield places much emphasis on research that is, in his terms, obviously relevant, with transparent connections to practical problems, links that can routinely be made obvious, and results that can be seamlessly integrated with their implications. Transparent connections and obvious relevance are even recommended as the appropriate guide for a scientist's choice of research questions. As a directive, however, the formula could benefit from fewer free variables, in that the criteria by which obvious relevance or transparency is to be judged are unspecified. (For example, are postreinforcement pauses on a fixed-ratio schedule obviously relevant to displays of aberrant behavior during periods of transition? Are parametric manipulations of delay to reinforcement obviously relevant to substance abuse or procrastination? Are studies of concurrent variable-interval schedules obviously relevant to understanding why interventions designed to increase a particular target behavior sometimes fail?) A contrasting view might hold that there can be little in the experimental analysis of behavior that is actually irrelevant to everyday human behavior, given the nature of our science.

Unlike hypotheses, theories, and models, together with the statistical manipulations of data which support them, a smooth curve showing a change in probability of a response as a function of a controlled variable is a fact in the bag, and there is no need to worry about it as one goes in search of others. (Skinner, 1969, p. 84)

Basic scientists do not exist in a vacuum just because their work is done under controlled conditions in the laboratory. They go outside too, live in the world, contact its problems and issues, and they see examples of our “facts in the bag” all around them. The necessary translational task then, it seems, is to help to identify for ourselves and others the role played by the “facts in the bag” of our science when dealing with socially important human behavior. As a start, we must tell the story, set the context, and make the argument for connections. Toward this end, Critchfield also highlights introductory comments in recent empirical papers, although he casts aspersions on “narrative interpretation” (p. 8). Beyond proximity to published data, the differences between these strategies are somewhat unclear, as is the basis for expecting differential persuasiveness. Setting a translational context is useful, however, even if it does not always persuade the general public, because it contributes to our science. When considered within a new or translated human context, new questions are raised and new variables are suggested. Thus, translational success cannot end with setting a context. Optimally, those bagged facts will be extended through the translational program. By way of example, although often quite clever, laboratory models of human phenomena are of limited value when they serve merely as demonstrations of complex repertoires. We need only look out our office windows to see complex human repertoires. The models take on considerable import, however, when used as a preparation for investigation of controlling variables. It is this intersection that seems truly translational, with basic science and human phenomena informing each other.

To be sure, there will be experimental questions best approached with a methodological “tool kit” that differs from the traditional strategies and tactics of pure basic behavior analysis. To come full circle, however, if direct practical benefits of our science are to be realized, the patient search for uniformities (i.e., facts in the bag) is likely to continue as the hallmark of translational behavior analysis, just as it has been for pure basic research.

What we call the scientific conception of a thing is not passive contemplation. When we have discovered the laws which govern a part of the world about us, we are then ready to deal effectively with that part of the world. (Skinner, 1953, p. 13)