There can be little question about it at this point: one signature of the current historical period for psychology and aging is an increased emphasis on the importance of applied research. The distinction between -- and the common separation of -- basic and applied research that typified psychological research traditions in the 20th century is becoming increasingly blurred. The current Zeitgeist is that a research program needs at minimum to be potentially relevant to real-world problems. In gerontology, this translates into doing more than simply describing age differences and age changes in psychological measures. There is mounting pressure (in the form of both reward and punishment) for psychologists in so-called "basic research" disciplines -- such as cognitive psychology -- to seriously engage the issue of applied research that benefits the quality of life for older adults.
For those of us who venture out of the ivory tower rarely (perhaps only to glance at a Division 20 Newsletter before going back into the lab), our assertion may seem surprising and horrifically inaccurate. An applied psychology of cognition and aging? The very label "cognitive aging" connotes to many the pursuit of basic psychological mechanisms associated with biological aging processes. Applications of knowledge gleaned such basic research, according to a traditionalist view, ought to be left to the softer (kinder and gentler) types! Although we believe it would be neither sensible nor profitable for all members of our discipline to engage in applied research, current trends will make it increasingly more important to consider issues of application and generalization of our research to the everyday life of older adults. We offer as supporting evidence for this claim these recent events:
(1) The creation in 1993 of the Edward M. Roybal Centers for Applied Research in Aging by the National Institute on Aging. One of the centers, focusing on applied cognitive psychology and aging, is housed at the University of Georgia and Georgia Tech. It involves the efforts of a number of scientists with basic and applied research interests (including Denise Park, Dan Fisk, Roger Morrell, Neff Walker, and Wendy Rogers).
2) The formation of a new society, The Society for Applied Research on Memory and Cognition (SARMAC), now associated with the journal, Applied Cognitive Psychology. The Society was formed in conjunction with the Third Practical Aspects of Memory (PAM) Conference (held in College Park, MD, last August). Next July the society will hold its first scientific meeting as a society in Vancouver, British Columbia. Aging research was well-represented at the third PAM conference, as it was in previous PAM conferences (see Hertzog & Dunlosky, in press), and one anticipates it will continue to be a topic of interest for SARMAC conferences in the future.
(3) The increasing emphasis on aging research among engineering psychologists and applied cognitive scientists, as reflected in research published in journals like Human Factors. Recently, APA created a new journal: Journal of Experimental Psychology: Applied. The journal represents an important new outlet for applied experimental work.
(4) The work by the American Psychological Society, APA, and related groups in forming the Human Capital Initiative, with a special task force devoted to issues associated with older adult populations (A.P.A., 1993). The task force identified a number of areas for targeted research that included attention to a number of applied research topics, including research targeting how to improve the quality and vitality of life of older adults.
What are the reasons for the current Zeitgeist? Briefly, we see them as increased demand and increased support. Our society is demanding more tangible benefits from federal and state supported research projects, and insisting upon concrete solutions to the societal problems that partly motivate and justify government spending to support research. We have successfully convinced John Q. Public that the greying of America has created enormous potential problems for our society. Concerns about the effects of aging, and on obtaining practically meaningful results regarding aging, filter up from citizens through public media, NIA Advisory Council, congressional hearings, and advocacy groups. The simple message is: "we want solutions to problems facing older adults in America today."
Our problem -- and one not to be underestimated -- is as follows. We may have difficulty convincing John Q. Public (much less ourselves) that much of the basic research agenda of psychologists is relevant to addressing those potential problems. Although a strong case can be made for the long-term practical benefits of basic research on aging and psychological problems, justification of deferring the pursuit of applied research questions in order to continue an emphasis on basic research becomes increasingly problematic in an era of federal and state budget cuts, disaffected taxpayers, and negative views of the role of government in American society.
This situation has in turn led to a subtle but important shift in emphasis in the kinds of research supported by private foundations and public agencies, like NIA. There is increased support available for applied research. As psychologists we understand very well the impact that such positive reinforcement has on the behavior of research scientists.
What is the appropriate model regarding research applications? Our colleague at Georgia Tech, Dan Fisk, has argued that "basic" research needs to be practically relevant (e.g., Fisk & Kirlik, in press). Dan is an exemplar of an experimental psychologist whose work integrates both basic and applied research questions. Dan's point, as we understand it, is that there ought to be a linkage between basic and applied research questions and results across studies in a research program. Not all questions, nor all answers, will be fundamentally applied in nature, but a linkage of basic and applied research thrusts enriches and informs both aspects of the enterprise.
In mulling this over, and discussing it between ourselves, we find the contrast of linkage to another metaphor to be instructive. Namely, the metaphor of leakage. According to the American Heritage Dictionary, leakage is defined as "an amount lost as the result of leaking." The notion of loss seems to us to capture the primordial fear of traditionally trained scientific psychologists: the quality of their work could be sullied, if not entirely blunted, by attending to issues of practical relevance and application. But more generally, leakage seems to characterize how someone might view "getting in on the action" with a minimal change in the nature of what one knows, does, or learns.
Faced with the inducements for applied research now being offered by NIA and others, a leaker (someone entirely different from you, dear reader, and ourselves), might reason thusly: "Hmm? how do we share the wealth emanating from this new applied vision thing? How do we cash in on the Zeitgeist with what we already got, by doing what we already do? How do we continue to justify doing what we've been doing by leaking a little over into this domain of applied aging research?" We hope our little parody does not offend -- clearly it captures the motivations of others who do not merit the support that should go to people like yourself!
More seriously, leakage connotes any minimalist attempt to recast results in terms of possible (often superficial) relevance to applied problems. The fundamental criterion for identifying leakage, as we chararcterize it, is that the concept of practical relevance cannot be translated into viable set of specific, explicit hypotheses regarding the applied benefits of the work. That is, leakage is characterized by an absence of a theoretically derived, logically plausible, and empirically justified system of arguments regarding the applicability of the work to solving real-world problems. If one cannot specify why, and in what way, the effects under study translate into direct application, then one is not linking the research program to applications.
Linkage, by contrast, represents a synergistic interplay between basic and applied research issues. Here research is focused on developing a progressive research program to address theory-based questions, with a major focus of the theory placed on real-life situations. The nature of the theory may need to be different than some theories concerning aging and cognition. Sole reliance on a global theoretical construct (e.g., age-related loss of inhibition) could lead to the generation of absurd and simplistic applied research questions. True linkage demands that the specific issues associated with a possible application -- such as the environmental context and personal characteristics of a targeted group of older adults -- must be carefully considered. Indeed, linkage requires both (1) a functional theory of psychological constructs (e.g., what are they used for? how are they manifested in everyday life?) and (2) sensitivity to the complex array of variables that one must consider in evaluating how real-world interventions may succeed or fail to reach a desired goal. Fisk and Kirlik (in press) refer specifically to the importance of theory-guided task analysis (as this concept is defined in human factors research), where the task in question is goal-directed behavior in a real-life context, and the analysis involves understanding the psychological mechanisms and processes that lead to success or failure in attaining that goal.
Three excellent examples of effective linkage in the existing research literature on aging and cognition are: (1) work by Karlene Ball and colleagues on the impact of age-related changes in attentional processes on the probability of automobile accidents, (e.g., Ball & Owsley, 1991); (2) research by Denise Park and colleagues on the role of age-related memory changes in influencing adherence to a medication regimen (e.g., Park, 1992); and (3) work by Cameron Camp and colleagues on using spaced retrieval techniques and external aids to assist everyday remembering by older adults with Alzheimer's Disease (Camp & McKitrick, 1992). What is characteristic of these three research programs is that the applied results both are informed by psychological theory and provide additional evidence regarding the viability of the theory. Applications are not merely a distal outcome, but an integrated part of the process of scientific discovery.
In our laboratory we have been working on problems associated with metamemory (cognitions about memory and memory-related processes) for some time. Although others in the field have explored how memory training interventions could be enhanced by restructuring cognitions about aging and memory (e.g., Lachman et al., 1992), our research program has not directly addressed the possible societal relevance and real-world applications of our findings. Recently, however, we have begun moving in the direction of practical relevance, and toward linkage with applied issues.
Some of our recent, as-yet-unpublished work (in collaboration with Lisa T. Connor) has focused on memory monitoring skills during learning. We have found evidence for maintenance of the ability to monitor on-going paired associate learning by older adults, even in the face of age-related changes in the rate of such learning. Indeed, older adults display near-perfect accuracy at predicting subsequent cued recall performance if they make a judgment of learning that is delayed for a few seconds after they finish studying a pair of words. This outcome suggests that older adults are capable of detecting when they have not learned a desired association (e.g., pairing a name with a face) and that they should be able, in principle, to use self-testing procedures based upon such judgments to effectively guide their learning. Subsequent experiments produced evidence that older adults indeed will differentially allocate study time in a multiple trial task according to experimenter-prompted monitoring.
Given existing evidence in the literature that many older adults may not spontaneously monitor their memory during study, our work provides a sound theoretical rationale for modifying training interventions to include a shaping of older adults' use of monitoring skills to assist everyday learning. This line of research therefore appears to be practically relevant. The proof of that assertion will be found in actual intervention research, which may tell as much, if not more, about the limits on applications of monitoring than the kinds of experiments we have run to date.
References
American Psychological Association (1993). Vitality for life: Psychological research for productive aging. Washington, D.C.
Ball, K., & Owsley, C. (1991). Identifying correlates of accident involvement for the older driver. Human Factors, 33,.
Camp, C. J., & McKitrick, L. A. (1992). Memory interventions in Alzheimer's-type dementia populations: Methodological and theoretical issues. In R. L. West & J. D. Sinnott (Eds.), Everyday memory and aging: Current research and methodology (pp. 155-172). New York: Springer-Verlag.
Fisk, A. D., & Kirlik, A. (in press). Practical relevance and age-related research: Can theory advance without application? In W. A. Rogers, A. D. Fisk, & N. Walker (Eds.), Aging and skilled performance: Advances in theory and applications. Hillsdale, NJ: Erlbaum.
Hertzog, C. & Dunlosky, J. (in press). The aging of practical memory: An overview. In Herrmann, D. J., Johnson, M., McEvoy, C., Hertzog, C., & Hertel, P. (Eds.), Basic and applied memory: Theory in context. Hillsdale, NJ: Erlbaum.
Lachman, M. E., Weaver, S. L., Bandura, M., Elliott, E., & Lewkowicz, C. J. (1992). Improving memory and control beliefs through cognitive restructuring and self-generated strategies. Journal of Gerontology: Psychological Sciences, 47, 293-299.
Park, D. C. (1992). Applied cognitive aging research. In F.I.M. Craik & T. A. Salthouse (Eds.), The handbook of aging and cognition (pp. 449-493). Hillsdale, NJ: Erlbaum.
To direct comments about the information contained in these pages, please write to marsiske@ufl.edu