A Model For Research Planning, in Consumer Behavior


Richard W. Pollay (1972) ,"A Model For Research Planning, in Consumer Behavior", in SV - Proceedings of the Third Annual Conference of the Association for Consumer Research, eds. M. Venkatesan, Chicago, IL : Association for Consumer Research, Pages: 594-601.

Proceedings of the Third Annual Conference of the Association for Consumer Research, 1972      Pages 594-601


Richard W. Pollay, University of British Columbia

[Richard W. Pollay is Associate Professor of Commerce and Business Administration at the University of British Columbia, and the Editor of the Journal of Business Administration.]

Despite impressive growth, it is arguable whether consumer behavior has yet established the research tradition and theoretical cohesiveness indicative of either a unique or a mature discipline. It seems we are still in the stage where, as a discipline. a struggle for a clear identity continues.

This position will need some explication, given the volume of literature being provided, and such is the purpose of the first part of this paper. It will be a necessity in this section, however, to be restricted to making some overview generalizations about the state of development of the discipline. It is not possible, no matter how desirable, to adequately review the substantive research in the field. That literature is simply too voluminous. That task will be left to the more ambitious, for it has been nearly five years since the last comprehensive review (Engel, et.al., 1968; Perloff, 1968; Sheth, 1967) and I have to agree with Perloff (1968) when he stated that the job of summarizing even three years of literature at an earlier stage of development of the "breathlessly changing field of consumer psychology is a task too Herculean for the reviewer to undertake" (p. 460). Thus this paper will not provide a summary of the state of knowledge, nor will it make any quasi-theoretical observations about the relationships between the knowledge in the various subareas, but rather will begin by a brief examination of consumer behavior as a science, examining its apparent productivity and progress.

The need for a comprehensive theory has been expressed in the literature repeatedly, and despite the admirable attempts to provide us with such a comprehensive theory, it retains its validity and deserves reiteration. The existence of a comprehensive theory is a necessary, although hardly sufficient, condition for the effective planning of research efforts, and it is this planning function that is the focus of this paper. Even in the absence of such a theory, however, it is possible to do some research planning. To put it another way, it is not inevitable that the development of the discipline be the haphazard result of fortune, idiosyncratic interests of the individuals involved, and methodological tractability. We can engage in a concerted effort to channel our energies into developing the kind of knowledge that may be most helpful in the development of the theory we seek.

To organize research activities meaningfully, it helps to have a means of readily comprehending the "state of the art". One such means is presented here: a topological conceptualization of accumulated knowledge. The full applicability of this model to consumer behavior research depends on the existence of a well articulated and accepted theoretical framework. This will be freely admitted; but the value of the discussion is not negated by the current lack of such a theory. The model precipitates some reorganization of thought, directing one's attention to the planning function in research programs. It also can be of obvious value in structuring research within the areas in which we have theoretical fragments.

Even if that were not the case, the discussion has value in the long run by preparing the way for effective research program planning once a more comprehensive theory starts to take shape. The analysis of the discipline's informational needs and the development of research strategies can, should, and

will be carried to more sophisticated levels than this introductory paper can even attempt. Effective research program planning can eliminate redundancy of effort, insure the production of aggregatable research results, and offer a fuller spectrum of information.


Judging by the volume of output, the study of consumer behavior is a healthy science indeed. But this veritable flood of articles, speeches, working papers and research reports is in itself a mixed blessing and not necessarily indicative of any evolution in the discipline--except a growth in the number of practitioners. One of the negative consequences is the simple problem of information overload. Put more precisely, "The dilution of the meritorious by floods of triviality makes the recognition of true scientific value particularly difficult" [This is, unfortunately, the case in most academic areas these days and is as much a reflection of the publish or perish criteria used by university promotion and tenure committees as it is a reflection on the state of the art in consumer research.] (Polanvi, 1958, p. 149). In addition, much of that published is research that was the "result of the availability of data, the convenience of research and mathematical techniques, and/or the appeal of certain behavioral constructs" (Kollatt, et.al., 1970, p. 328). But the ease of measurement is a poor criterion for selection of topics worthy of research. The exercise of measurement capabilities loses meaning when the existing theories are not highly directive toward objects of measurement. This is often insufficiently recognized, even, or perhaps especially, by those who call most vigorously for even more powerful measurement devices. As Sheth (1967, p. B719) notes, the "excursion into multivariate complexity presumes a formal understanding of the buyer". He might have explicitly added, that it was and is a presumption of very questionable validity.

None of the currently popular theories truly provide a key to adequate comprehension of the "data" being generated, although they may provide a mnemonic device for a cataloguing of such data. While the data bank has increased considerably, this has led to as much confusion as comprehension and we seem to witness more productivity than progress. Again, this results from the "paucity, and quite possibly the absence, of any theoretical under-pinnings which could give direction, meaning and permanence to substantive investigations" (Perloff, 1968, p. 437).

The status of marketing and consumer behavior as sciences is reflected in the very fact that the question is so very self-consciously and chronically addressed. That literature (Dawson, 1971; Halbert, 1964; Hunt, 1971; Lee, 1965; Robin, 1970; Sheth, 1967) of which this paper is guilty of being a part, has been disappointing and often has not attracted the best known scholars despite its importance. The asking of the question indicates our aspiration to be a science, but also our failure to realize that aspiration.

Kuhn (1962) discusses several behaviors which he holds to be indicative of something other than a normal science. In his terminology the following characteristics give corroborative evidence to the labelling of a discipline's activities as either "crisis science" or "preparadigmatic" activity: the proliferations of theories, or versions of theories; the expression of explicit discontent; the recourse to philosophy; the disagreement over the importance of "problems", a debate of fundamentals; a faster growth of complexity than accuracy; and professional insecurity among the scientists of the area. Since consumer research seems to possess nearly all of these attributes, [The text provides no argument that any professional insecurity exists within the consumer behavior field, although impressionistic observation suggests that it certainly does exist. An argument, admittedly weak in both structure and evidence, can be made. The tendency of the university professional in this area to publish for the sake of publishing, to be a professional academic, and to use publishability as his criterion of scientific value may be seen as indicative of professional insecurity as it betrays a lack of criteria intrinsic to the science. This insecurity may often be masked, however, by the tendency to pass flippant judgements on the value of others research, judgement often based on either the esotericism or the familiarity of the alternative research and not on conclusiveness precision or value of its results.] one is led to the conclusion that the study of consumer behavior is not truly a science no matter how much we may utilize what we perceive to be scientific methods. In Kuhn's classification, consumer behavior is in a pre-paradigm state. [Dawson (1971) erroneously concludes that marketing is a crisis science. In doing so he failed to recognize that to qualify as a crisis science there needs to have been a normal science with a well accepted paradigm, and the challenge of this paradigm by a competitive one. Since neither marketing in general, nor consumer behavior in specific, have either the history of a paradigm or a well articulated competitor, Dawson's categorization seems inappropriate. Dawson's confusion is also seen in his expression of fear that we "will lapse into the practice of normal science", (p. 72). (Emphasis added.)]

We are led once again to the conclusion that consumer behavior is sorely in need of theoretical improvements. This is hardly a novel conclusion and has been made in the literature repeatedly, perhaps best in the major reviews of the literature. Several other papers have discussed various aspects of the role of theory in consumer behavior and marketing. Halbert (1464) in an early paper discusses the requirement for a theory in marketing and describes especially well the requirements of syntactics, semantics and pragmatics. Hunt (1971) and Sheth (1967) offer classification schemes for theories as a device for assessing the status of marketing theory. Robin (1970) questions the ethical desirability of the developing positive science of marketing, although his ethical concerns seem limited as he focuses exclusively on the question of individual privacy as it clashes with the informational needs of a science. Dawson (1971) suggests that marketing may lose its inherent relevance as it becomes more scientific, but this paper is perhaps more valuable for its review of the concepts of Kuhn (1962). The single most comprehensive work for students of marketing is that by Zaltman (1973) and his discussion of metatheory.

A solid theory will provide several advantages. As a theory becomes well accepted, and therefore a paradigm in Kuhn's terminology, it provides the community of scholars with standard definitions for key concepts and variables, a common language of communication. Such definitions, and associated classifications, will permit an understanding of the dimensions along which results may be generalized, a need articulated by Kollat, et.al. (1970, p. 330).

Theory also permits the comprehension of large data fields and the integration of apparently diverse packages of information. For consumer behavior, like psychology, however, it is likely that "most useful theories will, for some time to come, be small conceptual systems dealing with a restricted range of phenomena", (Marquis, 1948, p. 434). The domain of behaviors that deserve explanation is simply so large that it would be optimistic and premature to expect a very powerful general theory. But hopefully theoretical developments, aided by increasing knowledge, will permit the gradual integration of such small conceptual systems into increasingly larger systems. This we do now by modelling, but the same result might be obtained in the future by the introduction of new concepts at a different level of abstraction that serve to unite and show communalities between currently distinct topic areas. As subsystems are amalgamated into a theory of consumer behavior, that theory will be increasingly integratable into an even more general theory of marketing.

Good theories are of primary value in the role they play in structuring research activities. Theories gain their acceptance by successfully "explaining" those problems perceived as most acute by the practitioners in the field - the previous anomalies. The theories also provide good definitions of problems and, importantly, offer a conceptual scheme that permits approach to those problems. Theories will be perceived as worth-while only so far as the practitioners perceive that the problems raised are solvable by operations within the theoretical structure, even if those problems are not yet solved. Without being able to presume the solvability of such problems the theory has little pragmatic value for the scientists.

Theory also facilitates specific research design, by identifying variables for control. The operation of theories generates testable hypotheses. Theories also permit the identification of needed research by, for example, identifying critical assumptions. "The more interesting and directly productive functions of theory in basic research, however, are those of coordination and planning" (Krause. 1971. p. 219). "A unified theory of consumer behavior may help to coordinate and control the specialized units by reducing the differences in goals and perceptions ..." (Sheth, 1967, p. B718). The heuristic role that theory plays in identifying research goals, and the establishment of goal priorities is a valuable one as it permits the planning of research programs.


To permit a science to evolve on an ad hoc basis, reflecting the idiosyncratic interests of its practitioners, the availability of data, and the convenience of measurement instruments, implicitly assumes that anarchical systems progress faster than do organized systems. Since few would hold that to be true in the political arena it is surprising that they appear to do so in the realm of science. But it is being increasingly recognized that "The organization of science is itself a scientific task, it is even a new science that has developed in our time; it is concerned with science and its laws, its development, its particularities, the general and specific aspects of its various disciplines, and its dependence on historical evolution and economic factors. In a word, science is the subject for scientific research" (Science and Synthesis, 1971, p. 151).

In the gathering of research information for the confirmation of theories one can conceive of three levels of planning and organizing activity. At the most microscopic level would be the experimental design; the design of a single experiment, although perhaps involving a number of treatment conditions of some complexity, aimed at determining the validity of one, or at most a few, assertions or hypotheses. At the other extreme, is what one might call policy design; the large scale planning of a "science", the selection of major alternative thrusts of a discipline. This is the level of planning that is at least implicit in the funding decision of large funds suppliers like the National Science Foundation. The decisions of who and what they support affect the character of the science that evolves.

But in consumer behavior there are few if any who have the opportunity and power to make decisions at that level, most of us face the more immediate research planning activities of our own private research ventures, and we have come to do so with some sophistication, at least at the first level described. Primarily because of our close association with market research techniques, we are trained to design experiments with great efficiency and precision, using the most elegant of designs, sampling techniques, measurement instruments, and the like. But there remains a level of research planning, obviously between the two described extremes, in which we do very little. That is the area of program design.

Program design is the "planning of an integrated set of projects focussed on a central problem" (Marquis, 1948, p. 431). That "problem" may for example be an hypothesis with the program aimed at discovering all of the conditions that are necessary and sufficient for the hypothesis to be valid. But it is a series of experiments, or research activities whose central thrust is some specific research problem. A fully developed research program would probably involve people with a number of disciplinary backgrounds, or at the least the problem would be attacked using a number of methodological approaches. A research program, unlike an experiment, expands the coverage of a research activity far enough to permit the examination for progress. [This is an explicit criterion because of the notorious failure of the academic community to be motivated by statements such as "what is now required is further research". Indeterminate research, which is the kind most frequently employing such a call for more research, is of no appreciable value and its unimpressive character is hardly a source of inspiration. The failure of other researchers to take up the lead provided is probably also the result of a once common practice of academicians to stake out a claim on a research problem by asserting that subsequent research was underway, even when the assertions had no basis in fact.] Program research is certainly more than the bleeding of a single project or data bank for a number of publications. It is also more than repeated application of a tool in search of problems. It is also more than the exercise of trivial variations on a successful theme. Programmed research is the attempt to be purposeful in some rational way; to address oneself to a research problem in an efficient and potentially fruitful manner. It involves replications and sequential experimental strategies (Cox, 1958). It involves all of the major phases of research activity, from problem formulation, through literature reviews, pilot testing, theoretical elaborations, to hypothesis testing. If successful, a research program generates the more information, with less redundancy of effort, time lost, operational vagueness, incomparability of data and general confusion. A well thought out research program certainly has more potential for information productivity than does an aggregation of individuals each leaping from whim to whim.


A most intriguing and productive way of thinking about the planning of research activities employs a topological conception of causal patterns, whether those patterns are supposed (theoretical) or actual (empirical). It is the kind of conceptualization that I personally find comfortable and convenient, but it also seems to be quite generally tractable and comprehensible, thereby allowing for further development and explication following this introduction to the ideas.

It seems valuable to follow the lead of Cox (1958) and to conceptualize a "response surface" which portrays the relationship between the phenomenon under scrutiny, the dependent variable, and all its causal factors, the independent variables. Such a surface is a k-dimensional generalization of a regression line, (or multiple regression plane) and the surface is simply that defined by the functional relationship between the dependent variable and all of the independent variables. Such a surface can and probably will take a variety of complex topological forms.

Let us however consider a response lattice rather than a response surface. This change hardly affects our thinking, but it does more accurately reflect the fact that many of our variables are discrete, especially independent variables that are experimentally fixed at specified levels. While the continuous model has certain appeals, it is rare that we can afford the thoroughness of research to approximate continuous measures on all of the variables. Let us also, just for the convenience of conceptual visualization, consider only three dimensional lattice with two independent variables as the base axis and the vertical elevation being the value of the dependent variable. In applying this model to an actual experimental program, however, it should be noted that it is essential that the early conceptualization of a lattice be expansive in its inclusion of factors or independent variables. This is so because the addition of a dimension to a response lattice at some date subsequent to the collection of research data makes the already collected data indeterminate along the new dimensions.

It is now possible to describe an experimental program by its location(s) within the lattice, the density and completeness of its coverage in some area, and the number of replicates undertaken. This is done by Krause (1967) who pursues the discussion to elaborate how such attributes will vary with different experimental purposes. The purposes he discusses are: the testing and qualifying or restricting a specific causal proposition ("scope restrictive"); developing a comprehensive causal proposition ("variance exhaustive"); and describing the efficacy of a specific set of treatments ("mapping"). That discussion will not be reiterated upon here. We will instead exercise this conception as a framework for discussion of research activities.

In any research program, the results of early experiments will have an influence on subsequent experiments. In fact, the conditionality of the latter experiments may be seen as a necessary component of truly programmatic research. All too many experiments are designed as if they were single-shot scientific excursions which will exhaust academic interest in an area. Recognizing that experimental exploration of a phenomenon is not so easily accomplished, suggests the importance of interpreting the early research in a programmatic manner, i.e., looking for its implications for future research. Informative early research is often informative because of what it tells us that we don't know, rather than what it tells us that we do know. The programmatic implications of early research are probably more important than the substantive findings and our evaluation of such research ought to reflect this.

In terms of the response lattice, what early experiments can do is to point the way to areas where the surface is irregular, complex, or ill-behaved. These can be thought of as "rough" areas. Early experiments also point to areas which are indeterminate, that is, where the variance of the dependent variable is high relative to the surface variation. These can be called "soft" regions. Possibly, but typically unlikely, early experiments will define surface sections that are both firm and smooth (well behaved). In these rare instances, the experiment does provide substantive information as well as programmatic.

Once the process of mapping a response surface has begun-s there are a number of strategies that can be followed. Perhaps the most difficult, expensive, and maybe the least valuable overall is the exploration of the rough surfaces. This process requires fine variations of the independent variables, but only over a limited range, and precise measure of the dependent variables. Alternatively, of course, one could "explore" the soft areas. This exploration usually involves the improvement of measurement techniques to increase reliability, or the introduction of new factors. Unlike the exploration of rough regions, it may not involve extensive experimentation over small ranges. It may involve replications of experiments at existing coordinates in the lattice, varied perhaps over some new dimension that will help "explain" the observed variation in the dependent variable. The last simple strategy is just to explore the completed undefined, currently unexplored areas.

Once the form and contours of the response surface start to take shape, and once that shape is firmed up by improved measurements and the aggregation of sample information, several strategic alternatives present themselves. Research programs might try to find maxima or minima, as is commonly done. They might also go through a search for sections of the surface that are the steepest, especially the steepest around a maxima. Such research answers the questions of "along what dimensions, or combination of dimensions, does the value of the dependent variable change the fastest?" or "to what independent variables is the phenomenon most sensitive?" One might also look for isometrics, the contour lines of the map of the surface to find out what alternative combinations of independent variables generate the same value of the dependent variable. Such a tactic, like the maxima search, might be valuable in pragmatic research as it would ultimately permit the more effective allocation of resources by creating what are in some sense indifference curves. Lastly, although this probably does not exhaust the alternatives, one might search for "firm" islands within soft regions. This identifies those sections of the surface where one can more comfortably predict what the relationship is between the independent and dependent variables.

The ability to pursue a program of research for the mapping of some response surface depends on measurement capabilities and the cost of research. It also depends, in a more basic way, on theory. Theory provides the research programs with suggestions about the important variables for inclusion in the factor lattice, suggestions about the locations of maxima, steepest ascents, and other topological features. It is rare, however, for a theory to be an explicit statement about the nature of the response surface. Many theoretical statements are certibus paribus in nature, describing the intersection of the response surface and a plane parallel to one of the axes. Or they may be generalizations, a description of the projection of the surface on one of the coordinate "walls". But even though the theories are rarely explicit statements of the functional relationship describing the surface, theories do provide direction for search. They do so by providing the researcher with an a priori mapping which is first a guide and then a foundation for the revision of that map in light of subsequent research results.

Theories, unlike maps however, always suggest features of yet uncharted regions. If they do not do so they are not valuable as theories and are only language transformations of existing knowledge, and not transformations into a more powerful language. The combination of good theory with a model for research planning is a powerful one, and it can both permit and encourage greater efficiency of research efforts.


Cox, D.R. The Planning of Experiments. New York: Wiley, 1958.

Dawson, L.M. Marketing Science in the Age of Aquarius. Journal of Marketing, 1971, 35, pp. 66-72.

Engel, J.F., Kollat, D.R. & Blackwell, R.D. Consumer Behavior. New York: Holt, Rinehart and Winston, 1968.

Halbert, Michael H. The Requirements for Theory in Marketing. In Cox, R. et al., (eds.) Theory in Marketing. Homewood, Illinois: Richard D. Irwin, 1964, pp. 17-36.

Howard, J. & Sheth, J. The Theory of Buyer Behavior. New York: John Wiley, 1969.

Hunt, S.D. The Morphology of Theory and the General Theory of Marketing. Journal of Marketing, 1971, 35, pp. 65-68.

Kollatt, B.T., Engel, J.F. & Blackwell, R.D. Current Problems in Consumer Behavior Research. Journal of Marketing Research, 1970, 1, pp. 327-332.

Krause, Merton S. Proving Causal Propositions: The Foundations of Program and Experiment Design. Multivariate Behavioral Research, July, 1967, pp. 349-376.

Krause, Merton S. Corroborative Results and Subsequent Research Commitments. Journal of General Psychology, 1971, 84, pp. 219-227.

Kuhn, T. S. The Structure of Scientific Revolutions. Chicago: University of Chicago Press, 1962.

Lee, C. E. Measurement and the Development of Science in Marketing. Journal of Marketing Research, 1965, 2, pp. 40-ff.

Marquis, D. G. Research Planning at the Frontiers of Science. American Psychologist, 1948, 3, pp. 430-438.

Nicosia, F. M. Consumer Decision Processes, Englewood Cliffs, N.J.: Prentice-Hall, 1966.

Perloff, Robert. Consumer Analysis. Annual Review of Psychology, 1968, 19, pp. 437-466.

Polanyi, Michael, Personal Knowledge: Towards a Post-Critical Philosophy. Chicago: University of Chicago Press, 1958.

Robin, D. P. Toward a Normative Science in Marketing. Journal of Marketing, 1970, 34, pp. 73-76.

Science and Synthesis. New York: Springer-Verlag, 1971. See Part 2, Ch. 4, The Organization of Scientific Research, pp. 147-178.

Sheth, Jagdish N. A Review of Buyer Behavior. Management Science, 1967, 13, pp. B718-B756.

Zaltman, Gerald. A Metatheory of Consumer Behavior, Forthcoming, (1973).



Richard W. Pollay, University of British Columbia


SV - Proceedings of the Third Annual Conference of the Association for Consumer Research | 1972

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