Presidential Address -- 1981:&Nbsp; Toward a Science of Consumer Behavior

Jerry C. Olson,
[ to cite ]:
Jerry C. Olson (1982) ,"Presidential Address -- 1981:&Nbsp; Toward a Science of Consumer Behavior", in NA - Advances in Consumer Research Volume 09, eds. Andrew Mitchell, Ann Abor, MI : Association for Consumer Research, Pages: v-x.

Advances in Consumer Research Volume 9, 1982      Pages v-x

PRESIDENTIAL ADDRESS -- 1981:  TOWARD A SCIENCE OF CONSUMER BEHAVIOR

Jerry C. Olson

[Jerry Olson is Associate Professor of Marketing at the Pennsylvania State University. During the 1981-82 academic year, he is on sabbatical leave as Visiting Research Professor at the Marketing Science Institute, Cambridge, Massachusetts. There are many people who have helped me see the issues addressed here a bit more clearly, both by our spirited discussions (arguments) and by alerting me to books and articles I otherwise might have missed. Among these, I am particularly indebted to Jack Jacoby, Andy Mitchell, Paul Peter, William lay, and Gerry Zaltman, and especially my students, past and present. Thanks are also due to Alden Clayton, Jack Jacoby, Paul Peter, and Diane Schmalensee for their helpful comments on earlier drafts of this paper.]

INTRODUCTION

Developing a presidential address is an interesting process. For one thing, it forces the writer to consider what he or she feels strongly enough about to warrant inflicting on a few hundred people for 30 minutes or so. Although the process was a bit painful, I did find something I felt that strongly about. It is reflected in my subtitle, "Toward a Science of Consumer Behavior."

I will continue the recent trend in Presidential Addresses in which ACR Presidents proselytize for their own ideas and values. My talk is also an attempt to convert some of you to wy way of thinking. I hope to convince most of you that the field of consumer research has problems with its theory. From what I've heard at this Conference, I don't anticipate any great difficulty doing that. However, I have no illusions that most of you will agree with my particular assessment of our theory problems or with the partial solutions I will recommend. At minimum, I want to challenge some of our traditional ways of thinking about research and theory and consider a few alternative approaches to developing theories of consumer behavior. I will be satisfied if you will think about these ideas h even if you ultimately reject them.

A SCIENCE OF CONSUMER BEHAVIOR?

I am not going to extensively defend the issue of whether we ought to aspire to have a science of consumer behavior. It seems to me that many (perhaps most?) of us either think consumer research is already a science or else we are trying to make it one. As my title implies, I am in the latter camp. I don't think we are quite there yet. But I do think that a science of consumer behavior is a worthwhile goal to pursue. I believe that many of us agree with Bill Wilkie (1981) in our aspirations to make consumer behavior more than an engineering-type discipline in which we apply concepts and theories developed elsewhere to solve specific problems. [Usually we tackle marketing problems. Occasionally we address public policy problems. Seldom do we directly concern ourselves with consumer welfare problems.] Although most of us to lots of engineering type work, many of us try to do science-type work, too.

What is science-type work? What would it mean to have a science of consumer behavior? Let me suggest that whatever else we think a science is, it has a lot to do with theory. Theories are a basic requirement for a science. To have a viable science of consumer behavior, we must have viable theories of consumer behavior. Thus, doing consumer behavior science involves working with theories - developing, testing, modifying, and improving theories of consumer behavior phenomena.

Current State of Consumer Behavior Theory

My basic contention is that we consumer researchers are not doing enough to develop theory. Moreover, what little theory development we to attempt is not being tone well enough. [Although this talk may have a holier-than-thou tone, I don't really feel that way. I recognize that I have been part of the problem. In fact, I am directing this talk as much to myself and my research behavior as to you.] Several previous ACR Presidents, among others, have pointed out many of the reasons why we find ourselves in this impoverished theoretical state. Jack Jacoby cited a long list of problems in our field, many of which concerned our poor work with theory. Hal Kassarjian, Jerry Kernan, and Dave Gardner all tried to focus our efforts on specific topics in need of better theory. Bill Wilkie discussed the kind of scholarly commitment necessary to make contributions to knowledge, which I interpret as contributions to theory. For the most part, these problems and the proposed solutions are widely recognized, so I will not review them here.

Instead, I want to discuss a research approach to developing consumer behavior theory that is neither widely known nor co only practiced. Although I believe this approach can help move us toward a science of consumer behavior, I recognize that it is at best only part of an overall solution to our problems. And I recognize that it is not for everyone. For one thing, this alternative research "style" requires adopting a somewhat different perspective on the procedures, methods, and philosophies of doing research than what most of us were taught in graduate school.

Why Is Theory So Important?

Before I elaborate on this research style though, let me deal with the counterarguments some of you already may be generating and try to convince you not to tune me out yet. Perhaps some of you are saying things to yourself like, "Oh no, another talk about Theory, with a capital T." Or, "I've got all these problems to be solved before 2:00 p.m.; I just don't have time to mess around with theory." Or the best one of all, "Don't give me a theory, just show me the data."

Please note that I'm not just talking about practitioners here. Many academic researchers have an inappropriately narrow view of theory, too. For instance, many of us tend to think that some of the things we do, do not involve theory. We may think that data, at least some data, stand alone. That is, we think some data are directly interpretable. We may think that some concepts are directly observable. These kinds of ideas reflect the basic underlying assumptions of empiricism and the positivist philosophy of science that still reigns in the social sciences (cf. Koch 1981) and in consumer behavior. This approach to research is based on the assumption that only our sense impressions - in research terms, our empirical observations provide useful knowledge of the world. It is as if characteristics of the world are sort of waiting around for researchers to come along ant observe them.

But these ideas have been repudiated by many philosophers of science. [In this brief talk I can not fully develop these ideas ant present them in a completely compelling manner. However, a few basic references have been cited to which interested readers can refer and form their own conclusions ant develop their own preferred style of inquiry. Suppe (1977) provides perhaps the best overall discussion of many of these issues. In fairness, there are philosophers who still adhere to many of the tenants of logical positivism, now reincarnated as critical rationalism (see Feyerabend 1975, Suppe 1977).] From their point of view, facts to not stand alone. Data to not have intrinsic meaning. No concept is directly observable. Even simple, apparently well-understood measures are based on complex, multichained, interconnected assumptions, which are really theories. Thus, in contrast to the empiricist perspective, this alternative view says that our abstractions -- our ideas, our theories - provide the basic framework and rationale for everything we do as researchers, Seven for our supposedly "direct" empirical observations. [The metaphysics of this point of view can be extended even further. The idea that theories provide the logical rationale for everything we do as researchers leads to the metaphysical position that our theories actually create the reality we observe. There are, at least in principle, an infinite number of ways in which we can theoretically represent some characteristic or phenomenon of the world. Therefore, there are an infinite number of alternative realities that we can create through our theories. (It may be easier to see this in other fields than in consumer behavior. Quantum theory ant particle physics are good areas to contrast with our field Two fascinating books that clearly illustrate these points are The Dancing Zu Li Masters by Gary Zukov ant The Tao of Physics by Fricof Capra.) This point of view clearly implies that we ought to be working to improve our existing theories and develop new theories rather than just trying to fit data to existing theories.]

Usually these theoretical assumptions are unstated. We seldom examine the "hidden" theories in our research; we seldom question them. [This is also true in psychology ant sociology, fields from which we borrow most of our theories. A clear exception, however, is the work of Ericsson ant Simon (1980) published in Psychological Review. Ericsson and Simon explicated the typically ignored assumptions underlying self-report behaviors and developed an explicit theory to explain certain aspects of self-reports.] Often they are very difficult to recognize simply because we have taken them for granted for so long. But these theoretical assumptions need to be explicitly recognized. Perhaps we would find that some of these theories are not justified or cannot be supported. Then we could begin the work to improve the theories.

Make Implicit Assumptions Explicit

So, one of the simplest things we can to do develop a science of consumer behavior is to make explicit as many of our theoretical assumptions as we can, including those that have been long hidden from our consideration. Certainly, we will have to stop short of examining every theoretical assumption. But even so, the practice can be very healthy. Some of you, of course, are already expert practitioners of this style - often to the chagrin of your students and/or your colleagues. It is a wonderful habit for all of us to acquire. It can make our thinking more rigorous ant precise, which should help us develop better theories of consumer behavior.

Our Current Use of Theory in Consumer Research

Perhaps some of you are a bit offended by this talk so far. Maybe you are generating counterarguments like: "Who's he talking about? I'm into theory' My studies always test some theoretically-based hypothesis!"

I grant you that overt concern with theory in consumer behavior has probably never been higher. Just look back at the literature of ten years ago ant see for yourself. Today nearly every article mentions some theory or another. Sometimes we even claim to be testing a theory! Hard-nosed business researchers ant "softer-nosed" public policymakers occasionally use theory to help make dec is ions . Why, we even have AMA Theory Conferences. And all of this has been going on for several years. But where is the progress in developing theories of consumer behavior?

In fact, we have become skillet at borrowing theories from other disciplines ant applying them to our problems. This is fine, but I am concerned with what we to with those theories after we have applied them. Seldom to we to anything beyond either applying them again or dropping them. Our discipline applies borrowed theory, but toes relatively little to develop theory. I echo the sentiments of Jag Sheth (1979), Jack Jacoby (1976), ant others who have called for an end to mere borrowing ant for beginning an extensive effort directed at theory development.

THEORY DEVELOPMENT

In the rest of my talk, I want to go beyond a simple plea for more theory development in consumer behavior. I want to present several specific suggestions for how a research approach that is intended to develop theory might proceed. [Let me be clear about my goals. Although I can be as evangelistic as anyone when I get started on a topic that interests me, I am not trying to convert everyone to this point of view. For one thing, it would be impossible. In a very interesting book entitled Methodological Approaches Social Science, Ian Mitroff ant Ralph Kilmann suggested that the style of inquiry adopted by a researcher is a function of many influences, including environmental, intellectual, ant social variables. Also, a researcher's preferred style of inquiry is influenced by his or her personality or temperament. Many of you may not find the ideas presented here compatible with your own ideas about research or your intellectual temperament. This is fine. In fact, Mitroff and Kilmann argue, I think convincingly, that a viable science involves several types of scientists, with different values, working from multiple theoretical ant methodological perspectives. A single approach is not sufficient to form a viable science. No one perspective has the inside track to "truth."] I think these suggestions have the potential to improve our theories of consumer behavior. But the improvement will necessarily be gradual. It will take time. Developing good theory is a very complex process. There will be deadends. Some ideas won't pan out. Basically, we will be involved in a trial and error process. We will have to begin modestly, but we must begin. To paraphrase Bill Wilkie's (1981) message last year, more of us will have to co it ourselves to contribute to theoretical knowledge about consumer behavior in order to make an impact.

Basic Assumptions Regarding Theory

In keeping with my recommendation that we make our assumptions explicit, let me state the basic assumptions about theory that underlie the rest of my talk.

I consider (at least this year I do) theories to be representations, abstract conceptualizations that represent the phenomenon of interest. The phenomenon of interest can be virtually anything - a measure, a method, a data analysis procedure, a simple behavior, or a very complex behavior. There are, of course, many alternative ways co represent any event or phenomenon. Thus, there are many possible theories of anything. Any single theoretical representation will be flawed in that it will be incomplete; it will not capture all of the aspects of the phenomenon. In other words, we know from the beginning that our theories are problematic. This idea can cause a subtle (or perhaps not so subtle) change in our typical perspective on theory and scientific research. A researcher who adopts this perspective may become less interested in testing theory. Rather, a researcher who sees all theories as imperfect representations tends to be more concerned with developing or improving theory, with trying to produce better representations of the domain or phenomenon of interest.

OK, but what is "better"? A better theory is not necessarily one that can be verified by data or that successfully survives some falsification attempt. Alternative theories could also be verified or avoid falsification. Rather a better theory is a more useful representation. But useful for what? Well, useful for whatever purpose it is you are theorizing about. For example, a theory may be useful for helping suggest solutions to a problem, or useful for explaining large bodies of complex data, or heuristically useful for generating new theories or stimulating new research directions (cf. Gergen 1978). Although we could argue about which aspect of usefulness is relevant for a particular case, these are all viable ant appropriate criteria for evaluating theories. But they are not widely used as criteria in most of our research.

Instead, the dominant approach to theory research in our field seems to be concerned mainly with whether empirical data "fits" a theory (or vice-versa). Generally, we test theories against data. More specifically, we usually "test" a theoretical prediction of "X" effect by comparing it against the null of no effect. Because the null is seldom given any theoretical meaning, all we have is a theory that predicts obtaining some effect, in contrast to a strawman null. Most of our studies, therefore, boil town to simple demonstrations that the anticipated effect was obtained. Much less frequently we try to "falsify" the theory (cf. Calder, Phillips, and Tybout 1981). Although both of these types of research may be useful and appropriate for certain purposes, I argue that neither approach has been very useful for developing new theory or for producing valuable modifications of "old" theory.

A null-hypothesis-testing style of research has m ny other dysfunctional consequences for developing a science of consumer behavior. [There is a sizable literature that should convince you of this point, if you to not already agree with me. If you are not familiar with it, why not take a look ant form your own conclusions? For starters, see Bakan (1966), Greenwald (1975), Lykken (1968), Mheel (1967), and Platt (1964).] One is that it focuses the researcher's attention on obtaining statistical significance rather than on the magnitude of the effect itself -- e.g., the strength of the relationship -- which is more relevant to its usefulness. [Occasionally, I have seen papers in which only the size of the obtained p values were reported. No mention vas made of the absolute magnitudes of the effects themselves.] A more serious problem is that sometimes we get lazy ant let the results of our statistical inference analyses to our scientific inferencing or theorizing for us. Too often, we are content to let a statistically significant effect stand alone. We try to let the data "speak for themselves," something that data can not really to.

A Different Style of Inquiry

My major suggestion for breaking out of these patterns of behavior is that some of us adopt a different style of inquiry for at least that part of our research effort intended to develop theory. We need a research approach in which theory development, rather than merely collecting empirical support for a theory, is the primary goal. For such objectives, the traditional views on empirical research are not very useful.

Null Hypothesis Testing. In particular, we should move away from a style of research based on simple null hypothesis testing. At best, such studies can provide only weak evidence about the usefulness of a theory. Moreover, they to not tent to generate the conceptual speculations that are necessary to modify and improve the-theory.

Strong Inference. As an alternative to a style of research based on simple verification or falsification doctrines and carried out by null hypothesis testing procedures, we might adopt (or adapt) a style of empirical research described almost 20 years ago by John Platt (1964) in an article entitled "Strong Inference." Basically Platt suggests that we should pit competing hypotheses against one another where each is based on a different theory. Thus, in the ideal study, one theory will be supported ant the other will not be. Such outcomes provide an empirical basis for making strong inferences about the usefulness of both theories.

In other words, in our empirical research we should test theory against theory, not theory against data. We should also be more concerned with comparing theories with each other at a conceptual level. As we become more familiar with this style of thinking ant research, we will become more skillet at identifying the contradictory features of alternative theories, some of which are likely to be implicit, metatheoretical assumptions. Then we can design better studies in which these discrepant features are compared against each other. If a test is well designed, we may have a critical experiment that clearly establishes the superiority of one idea over another.

An interesting wrinkle in this kind of study was recommended by Paul Feyerabend (1977), who suggested that we not drop the "losing" theory in such contests. Rather, our post-experimental efforts should go into modifying and improving the loser, as well as the "winning" theory. In other words, we should continually work to develop and improve alternative, competing theories, not just our favorite theory, not just the one enjoying general support at the moment.

Bootstrapping. I also believe that we need to analyze our data more deeply, more carefully and more intensely. I mean this in both a theoretical, conceptual sense and in a statistical analysis sense; however, I am not advocating more sheer number crunching. If our goal is to develop theory, then we will need better - i.e., more conceptually sophisticated - data about which to speculate in order to modify and improve our theories. Then, these improved theories can guide the collection of even more sophisticated data, which in turn can be used as a speculative basis for further developing the theory. And so on.

This approach to doing science and developing theory is called bootstrapping, and is described in Theory and Evidence, by Clark Glymore. Although this style is different from the traditional scientific method, there is fairly convincing evidence that successful theory developers follow a bootstrapping approach. Bootstrapping may seem uncomfortably like "cheating" to some of you. But not if you take the point of view that all theories are imperfect representations, and our objective is to develop better representations. From this perspective, the bootstrapping approach is quite appropriate for developing theory_

Proliferate Theories

Another, perhaps more controversial suggestion is related to these ideas. Rather than seek a single, overall theory - 8 single paradigm to tie the discipline together -- we might intentionally proliferate theories. Especially given our present state of ignorance about consumer behavior, we should not rush to one point of view, to one paradigm. Real knowledge and understanding (not just apparent knowledge) is most likely to come from the application of many alternative points of view (cf. Feyerabend 1977). [This is similar to the yin and yang principle of oriental philosophies, which suggests that extreme contrasts are necessary for understanding (cf. Capra 1975).] This is another way of saying that we will learn more by comparing theoretical ideas with alternative theoretical ideas than by fitting data to single theoretical ideas.

Where are we supposed to get all of these alternative theoretical ideas? For one thing, we can start by doing more speculating. We should be speculating about the theoretical assumptions underlying our measures, our experimental procedures, and our analyses. In particular, we should do more speculating about the meaning, actually the alternative meanings, of our results. [I'm not speaking to only my fellow academics here; applied researchers should do more speculating, too.] Based on these speculations, new theories may develop and existing theories may be modified. Let's not be afraid to do it, and let's not dump on those who try.

Where else, besides our own speculation, can we find alternative ideas to contrast with our theories of interest? Feyerabend goes further than most of us are probably willing to go by suggesting that we look to the most eccentric sources for alternative theoretical perspectives. For instance, we could look to Voodoo magic as an alternative to the germ theory of disease to explain why people get sick and sometimes die. Or, we could proceed counterinductively, as Feyerabend puts it, by intentionally postulating irrational theories and treating them as serious alternatives to our theory of interest. Consumer research may not be ready for such extreme steps, but there are less bizarre sources to which we can turn. We can generate alternate theoretical ideas from workable solutions to applied problems, from obtained data, from the theories that we borrow from other disciplines, and from everyday life.

As comforting (and seductive) as it is to have a widely accepted paradigm for conducting our research, we should tolerate and even encourage the gadflies among us to core up with alternative perspectives that r y not square with our common sense. Moreover, we should publish these ideas if they are well-reasoned and clearly presented (i.e.S if they precisely describe how they differ from better-known theories). By comparing these alternative theories with each other, both at a logical conceptual level and at an empirical level, we will have a strong inference basis from which to work to develop both theories. In this sense, a plurality of theories and research paradigms, instead of a monolithic theoretical structure, can be seen as beneficial and as a positive indicator of progress toward a science of consumer behavior

Address Bigger Issues

My next suggestion concerns the focus and content of our theorizing and our research. Although there are notable exceptions, to be sure, many of us need to tackle "bigger" issues. By bigger, I mean more important issues that make a difference, issues that have broad ramifications at a theoretical level or broad implications at an applications level. Too much of our research and theory is concerned with "small" issues, issues that don't make a great deal of difference either for theory or for applications. [This may be the most frequent criticism of academic consumer research by practitioners, and of applied research by theoretically-oriented researchers.]

We seem to prefer to study " . . . problems, theories, or research paradigms that appear simple ant are easily studied rather than the more basic and important problems that are invariably complex and difficult to resolve" (Battig and Bellezza 1979, p. 322). Does the following passage in which the late Bill Battig describes the typical "development" in cognitive psychology ring true as a descriptor of our own "progress" in developing a science of consumer behavior?

"First somebody comes up with a new theory, research paradigm, or interesting ant controversial empirical result, which appears quite simple, straightforward, and easy to investigate further. This catches on, creating a new 'hot' research topic, which promises to be more productive than previous approaches, ant therefore attracts the interest of a great many psychologists. But as more work gets done, the originally simple problem gets more complicated, because of failures to replicate the original findings, demonstrations that the original problem is inadequate or at best incomplete, ant increasing evidence that the problem is more complicated and less general than originally thought. So as this relationship develops, it becomes apparent that any further progress will require a great teal of painstaking detailed research activity directed toward limited aspects of the overall problem or phenomenon as well as efforts to interrelate the topic appropriately with other previously distinct topics or phenomena. In other words, further research has reached a point of diminishing returns, because a threshold of too much complexity has been crossed, so the once hot topic now appears nonproductive or uninteresting, ant soon ties out to be replaced by one or more different more simplistic types of research. So then the cycle starts all over again, often with almost total suppression of everything that was done or learned in the context of the previously 'hot' research topic." (Battig and Bellezza 1979, p. 323).

In the brief 20-25 years of major research effort regarding consumer behavior, how many times has this happened? Think of all the theories, concepts, hypotheses, and ideas that have been dropped from favor when the going got tough. many of them probably prematurely. For starters, how about motivation research, stochastic modeling, perceived risk, brand loyalty, and attitude theory? Will attribution theory, information processing theory, causal modeling, or the next "hot" idea not yet even on the horizon go the same way? Probably, unless we begin to see our task as developing and improving these theories, rather than as testing them in the sense of finding one that seems to fit the data. Until more of us stop seeing consumer behavior as an engineering-type discipline and start seeing ourselves as scientists concerned with developing theory, I don't think we will make much progress.

Don't Drop Theories Prematurely

My next suggestion expands on this one. Perhaps we should not be so quick to drop a theory that runs into trouble. The trouble could be conceptual in that the theory has some vague aspects, or isn't elegant, or doesn't explain certain phenomena very well. Or, the trouble could be empirical in that the theory is not consistent with certain aspects of the data. But all theories have problems. [Alternatively, most theories (even bizarre ones) probably have some value. At minimum, any theory can be useful as a counterpoint to a more reasonable theory.] In fact, such problems are expected, when we think of theories as imperfect representations. So, the idea is to give a theory lots of chances to show us its virtues, along with its faults.

As Thorton Roby (1959) suggested, "Suggestive hypotheses should not be put directly to drudgery but should be entertained for awhile, as rare and welcome guests (p. 131)." Perhaps we should become a bit less concerned about whether we can produce data to support a theory, especially early in its life cycle. Early attempts to make data fit a theory are often disappointing. The resulting dissatisfaction can cause researchers to move on to other theories. But premature rejection of an idea with merit is a very serious error in terms of theoretical development. It is a kind of Type III error, which to the theory developer is much more important than the Type I and II errors of primary concern to the empirically-oriented researcher. The Type III error is more critical because it tends to stop investigation altogether on ideas and concepts that may have merit.

I am not saying that a theory should not have to account for data. Useful theories should account for data, eventually. But there is an appropriate time and place to rigorously apply this criterion. A new theory may have to wait, perhaps for many years, until the necessary measuring procedures can be developed. Or, the theory may have to be modified, or better supportive data developed, perhaps using a bootstrapping approach.

More Tolerance

My next suggestion concerns the tolerance in our field that is necessary in order that a variety of theoretical perspectives can flourish. All of us, but especially journal editors and reviewers, need to be more tolerant of new theoretical ideas. [The field of consumer behavior has always been an eclectic discipline; thus, we are probably somewhat more tolerant of new ideas than other, more insulated fields of study. However, I don't think we can be characterized as highly tolerant of new ideas, or of their proponents. There is room for improvement.] The need for tolerance will increase as our discipline continues to mature. Specialized subareas of interest in consumer behavior are beginning to crop up now and will continue to develop. We should welcome these diverse views and encourage their proliferation. But we must guard against the champions of these specialties becoming so polarized and isolated from one another that there is no communication, no understanding, and no tolerance. Let's not get into the kinds of situations common in many of the disciplines from which we borrow - the "You're-either-with-us-or-against-us" syndrome. All types of researchers, with different perspectives ant different preferred styles of inquiry, are necessary to develop a science of consumer behavior. We need the empiricist, the humanist, and the theorist. We need people interested in data analysis, methodology, modeling, marketing, psychology, sociology, and philosophy. But to make it all work, each person needs to understand the perspectives of the others and appreciate their contributions.

A Non-Marketing Perspective

My final suggestion is somewhat more specific. I think that we should expand our beginning efforts to develop concepts and theories of consumer behavior from different perspectives than that of the marketing manager. For instance, what would a theory of brand loyalty look like from the perspective of the consumer as an effort minimizer? Or, what would individual difference theories of consumers be like if they were not consciously constructed to be useful for market segmentation? Until we start explicitly contrasting our marketing-oriented theories with theories based on different values and objectives, we probably won't realize how limiting the marketing perspective is.

CONCLUSION

In conclusion, the field of consumer behavior research has made progress and continues to mature. But how will our future progress be charted? Will we continue to borrow theories that have enjoyed success in other disciplines and adapt them to a consumer behavior context? Will we then be content to run demonstration studies in which we attempt to show that these theories are at least somewhat consistent with our data? Or, will we develop the conceptual skills, the necessary styles of inquiry, and the courage and self-confidence that will enable us to further develop these theories and to create our own theories? I hope we will not be afraid to modify, extend, and improve the theories we borrow. I hope we will encourage those who can to boldly speculate about consumer behavior phenomena. I hope we will nourish ant develop these theoretical ideas, because they are necessary for us to mare toward a science of consumer behavior.

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