Interpretive, Qualitative, and Traditional Scientific Empirical Consumer Behavior Research


Bobby J. Calder and Alice M. Tybout (1989) ,"Interpretive, Qualitative, and Traditional Scientific Empirical Consumer Behavior Research", in SV - Interpretive Consumer Research, eds. Elizabeth C. Hirschman, Provo, UT : Association for Consumer Research, Pages: 199-208.

Interpretive Consumer Research, 1989     Pages 199-208


Bobby J. Calder, Northwestern University

Alice M. Tybout, Northwestern University

There can be little doubt that, at this stage in the development of consumer research, methodological pluralism is desirable. Although, we believe, that traditional scientific empirical research on consumer behavior has made progress, it would clearly be difficult to argue that it has enjoyed sufficient success to preempt other approaches. Our premise at the outset of this analysis is that other approaches should be explored and methodological pluralism encouraged.

To embrace methodological pluralism ought not to imply, however, that all approaches to consumer research should be treated similarly. We contend in fact that methodological pluralism can only work if the differences between different kinds of studies are recognized and the strengths and weaknesses of each approach are assessed in terms of these differences. The alternative is not pluralism but methodological babble.

We have proposed a framework (Calder and Tybout, 1987) for grouping different approaches so that their unique strengths and weaknesses can be discussed relative to the nature of a particular approach. In the present analysis we will elaborate on this framework and then use it to comment on three important issues we see arising from the present volume. We will not attempt a micro-level critique of individual studies, believing that this is premature given the acknowledged preliminary nature of much of the work. It is not premature, however, to focus on the broader methodological issues raised by studies using new approaches.


Researchers have used a variety of labels in introducing new approaches to consumer research: interpretive, naturalistic, qualitative, humanistic, and the like. The Calder-Tybout (1987) framework seeks to reduce these to three broad classes of research: interpretive, qualitative, and scientific. [For the purposes of this chapter, we will be referring to the three tyWs of knowledge and their respective implied methodologies as general "approaches." In an effort to make the labels for the approaches intuitively meaningful, we use the descriptors interpretative, qualitative (rather than everyday) and scientific. For a more detailed discussion of the types of knowledge an their implied methodologies the interested reader is referred to Calder and Tybout (1987).] This is not to say that other labels do not carry important distinctions. Our contention is only that (a) these three classes have integrity at a general level and (b) are sufficient for making some important methodological points.

Each approach is best characterized in terms of the type of knowledge it seeks to produce. The goal of the interpretive approach is an understanding of behavior in terms of a particular system of ideas and from the frame of reference of these ideas. Data are made meaningful by virtue of the application of these ideas, and this gives rise to "interpretation" as the most general label for this exercise. Interpretations are proposed and evaluated among a community of scholars sharing the particular system of ideas. We have argued that this methodological process seems consistent with a philosophy of critical relativism, although problematic issues arise in this regard (Hunt, this volume).

The goal of the qualitative approach is an understanding of behavior in terms of how consumers themselves interpret and give meaning to their own behavior. Data are considered to be self-reflexive. They supply their own meaning. Researchers attempt to articulate how consumers explicitly or implicitly view themselves on the assumption that these views will shape subsequent behavior. 'Me appropriate methodology is thus to come into sufficient contact with the consumer's world to experience it as the consumer does (Calder, 1977). The appropriate philosophy is the common sense World of everyday ideas.

The qualitative approach can obviously be viewed as a version of the interpretive in which behavior is being interpreted from the standpoint of the ideas of consumers. We believe, however, that separating the two is useful. Applying a system of ideas that consumers may never even have heard of versus discovering the ideas that consumers use are very different enterprises.

The goal of the scientific approach is to understand behavior in termstheories that have been subjected to rigorous empirical testing. Although theories provide interpretation, the key point is that theories are capable of and have been subjected to empirical testing. Interpretation is a matter of theory application and is derivative of empirical theory testing (see Calder, Phillips, and Tybout, 1981).

We have argued that the methodology of rigorous empirical testing is best guided by a particular version of sophisticated falsificationism (Calder and Tybout, 1987). Theories should not be regarded as proven or true. They have scientific status because of and subject to attempts to refute them. The practical process of attempting to refute theories is of course itself fallible. Researchers can be mistaken about data. Nonetheless, the guiding objective is to test theory against data.

The main question that arises from the Calder-Tybout framework is whether, even at this level of generality, the three approaches can be differentiated. Anderson (1983, 1986, and this volume), for instance, contends that the scientific approach cannot be distinguished from other approaches. He argues that philosophers of science continue to debate the demarcation of science form non-science and that the falsificationist view is not universally accepted. In particular, falsificationists have not dealt at an operational level with the problem of fallible data. Because there is not agreement, and everyone recognizes that data may in practice be fallible, it is argued that no demarcation of science is possible.

Our position is that the fact that demarcation is in practice fuzzy does not mean that demarcation is in principle useless. Our use of falsificationism has always been as a guiding objective that characterizes the nature of the scientific effort. Perhaps communication is best served by illustrating the spirit in which we distinguish scientific from other approaches. A recent comment by Stephen Hawking, arguably one of our greatest scientists, captures this spirit well.

Any physical theory is always Provisional, in the sense that it is only a hypothesis: you can never prove it. No matter how many Limes the results of experiments agree with some theory, you can never be sure that the next time the result will not contradict the theory. On the other hand, you can disprove a theory by finding even a single observation that disagrees with the predictions of the theory. As philosopher of science Karl Popper has emphasized, a good theory is characterized by the fact that it makes a number of predictions that could in principle be disproved or falsified by observation. Each time new experiments are observed to agree with the predictions the theory survives, and our confidence in it is increased; but if ever a new observation is found to disagree, we have to abandon or modify the theory. At least that is what is supposed to happen, but you can always question the competence of the person who carried out the observation. (Hawking, 1988, p. 16)

The boundary between science and other approaches in our framework is meant to reflect the spirit of Hawking's comments. As a matter of normative principle, the scientific approach is fundamentally oriented to challenging theories with data. Use of the word "scientific" of course can connote many other things. Not the least of these is that the scientific approach is necessarily superior to other approaches. Although there is nothing in our use that implies this, it may be useful to soften the label by referring as we do here to traditional scientific empirical (TSE) studies of consumer behavior. In any event, we again assert that we do not intend to preclude other approaches by demarcating the scientific.

Likewise, we would resist the use of terms such as post-positivist to characterize other approaches. Such labels imply the demise of traditional scientific empirical studies. Methodological pluralism is again best served by not defining any approach as precluding another approach. Moreover, as Calder and Tybout (1987) point out, the term positivist is used much too loosely to be descriptive of any approach. Further, as Hunt (this volume) notes the historical meaning of the label "positivist" is incompatible with the TSE studies to which it is often applied.

The other boundaries in the Calder-Tybout framework are also intended to provide normative guidance. Calder (1977) has discussed the demarcation of the qualitative approach from the scientific. In practice it may be very difficult to say whether a specific study is scientific or qualitative. And the tendency to dress up any piece of research in the cloak and trappings associated with scientific theory is hardly helpful. In principle, however, the research goals are very different.

The Calder-Tybout framework can be used to analyze three important issues that cut across the present volume. The first is the contention that critical relativism, a view that we have argued might serve as a methodological base for the interpretive approach, should instead be adopted as a more general philosophy and a challenge to our framework. This claim is related to the view already discussed that the scientific approach cannot be distinguished from other approaches. The specific issue to be addressed in more detail is the critical relativists' attack on traditional scientific empirical studies. We will argue strongly for the central role the TSE approach gives to challenging theory with data. The second issue concerns the need to draw stronger conclusions from qualitative research and while doing so to avoid going beyond consumers' perspectives to another system of interpretation. And the third issue concerns the tendency to stretch the interpretive and qualitative approaches beyond research and into expressiveness.


Before turning to issues that more directly relate to the general purpose of this volume, we focus upon the two chapters, one by Anderson and one by Peter and Olson, that have as their primary objective discrediting our distinction between the scientific and interpretivist approaches. Although we recognize that the detailed rebuttal we present may be of only limited interest to a general audience, the strongly worded and largely unsupported conclusions advanced by these critics leave us little choice but to devote a portion of this chapter to answering their charges.

Scientific Knowledge and the Demarcation Issue

As mentioned in the introduction, demarcating science from non-science has come under attack. Here we address some of the more specific concerns raised. Anderson's objection to demarcation stems from the observation that philosophers of science cannot agree on a basis for creating such mutually exclusive categories. He worries that our criteria of confronting a theory with data that could reveal its weakness, and accepting as scientific those theories that succeed in providing a better account for the data than available rivals, would require that we consider parapsychology "science". Hunt (this volume) provides an excellent and detailed response to Anderson's anti-demarcation argument, so we will only reiterate his observation that "Most, if not all, genuine and useful categorization schemata have borderline cases (Hunt this volume, p. 192)," and add parenthetically that if a theory that some might label as parapsychological does survive rigorous testing procedures, and credible rival explanations for the phenomena it explains cannot be generated, then perhaps this particular theory (not any or all parapsychological accounts) warrants the label science.

By contrast, Peter and Olson evidence concern not for what our demarcation would include in the domain of scientific knowledge but rather for what it might exclude. Specifically, they contend that invoking a falsification criterion for scientific knowledge would lead to excluding from the domain of science the work of Newton and Einstein, general models of consumer behavior such as the Howard and Sheth Model, and mathematical models of consumer behavior. These inferences do not follow logically from the position we advance and suggest that Peter and Olson are confusing researcher's personal motivations and behavior with the status of the knowledge they create. It is well documented that individuals, both in their role as researchers and as everyday consumers, evidence a tendency to seek confirmation for their views rather than refutation. However, scientific status should not, and typically is not, accorded to claims unsupported by data that could contradict them. That is, researchers rarely, if ever, succeed in gaining acceptance for their theories on the basis of data they alone collect in a confirmatory fashion. Typically they must account for the data of others and phenomena observed in the world at large. Theories such as those of Newton and Einstein gain acceptance for precisely the reason that they explained phenomena for which previously there was no good account, and it is in this sense that they survived "falsifications", or perhaps a more accurately, survived attempts to reveal their weaknesses. Thus, in our view the motives of the theory creator or champion are not per se pivotal in judging the theory, though they could render certain rival explanations more plausible thereby calling the theory into question. The theories advanced by Newton and Einstein met our criteria for scientific knowledge at a point in time -- they accounted for phenomena better than their available rivals. Whether they continue to be accorded scientific status depends on their ability to account for new data that become available. Notice that because we see no inherent superiority of post hoc over a priori explanations of phenomena, data already available at the time a theory is developed afford valid tests of its adequacy. (See Sternthal, Tybout and Calder 1987 for More on the post hoc versus a priori distinction.)

However, Peter and Olson are correct in inferring that some general models of consumer behavior and some mathematical models may not meet our criteria for scientific knowledge. Each model requires its own assessment. "Box and arrow" or flow chart models may be valuable frameworks for integrating scientific knowledge without necessarily themselves being scientific. They may be more usefully viewed as systems of hypothesized relationships, some of which may be neither well-specified nor tested empirically. On the other hand, one can also imagine a general model of consumer behavior that is itself scientific because it is grounded in empirical tests of all the relationships hypothesized. This would not require that all relationships be tested simultaneously, rather multiple experiments, each exploring a subset of the hypothesized relationships might serve as evidence for the model. Likewise, mathematical models may or may not be scientific depending upon how they are constructed and whether they are superior to available alternatives. Certainly some modeling efforts, such as applications of LISREL, have the potential to yield knowledge we would consider scientific.

The more general concern that Peter and Olson appear to have is that, under our framework, all of consumer research would not automatically be considered scientific. We wonder why such a notion is so troubling? As we consistently have argued, interpretive and everyday/qualitative knowledge are not inherently more or less valuable than scientific knowledge. The three types of knowledge merely are generated with different goals in mind and therefore should be judged according to different criteria. Holbrook and O'Shaughnessey (1988) express what may be motivating Peter and Olson's concern--the fear that knowledge not failing under the heading of "science" be viewed as unpublishable in the leading journals in the field. We would hope that such a concern is unwarranted. After all there are many prestigious journals that make no claim of presenting scientific knowledge in fields such as the humanities. However, whether or not different types of knowledge should be represented in a single journal such as the Journal of Consumer Research or whether multiple outlets would be more appropriate is not for us to say. It is an issue that deserves discussion among journal editors and their editorial boards. What should be clear, however, is that little is solved by arguing that all types of knowledge are scientific. The need for demarcation, problematic as it may be in classifying some specific cases, seems clear. Indeed, it is interesting to observe that the criticism of demarcation in this volume focuses on our distinction between scientific and interpretive knowledge, suggesting tacit acceptance of the demarcation between scientific and everyday knowledge. Of course, logically, one cannot reject the possibility of demarcation and exclude any knowledge from the domain of science.

Normative Criteria and the Sociology of Science

The issue of demarcation is related to a second criticism, which centers on whether our version of sophisticated methodological falsification (SMF) either should be or is the methodology of scientific knowledge. Because it would be naive for us to argue that all knowledge generation would be well served by SMF, this discussion presupposes the possibility of demarcation and the goal of creating scientific progress.

Anderson contends that sophisticated falsificationism fails to offer an accurate account of the history of science and it also does not provide (nor was intended by Lakatos to provide) normative criteria for conducting research. Peter and Olson echo these sentiments and raise specific normative questions they believe falsificationism leaves un-answered. Several points need to be made in responding to these charges. First, although the history and sociology of science is a fascinating topic to discuss, it was not the topic of the Calder and Tybout (1987) paper. Thus, the observation that individual researchers don't necessarily behave like "good falsificationists" is simply an acknowledgment of the sociological forces at work and is not itself damaging to the normative contention that the SMF methodology is the one most likely to serve the goals of science. Moreover, our version of falsificationism is actually more consistent with the general evolution of theories (though not necessarily the behavior of individual scientists) in fields such a physics than Anderson and Peter and Olson suggest (see Hawking, 1988).

Second, we are less concerned with Lakatos's intentions for sophisticated methodological falsificationism than we are with how some of the general notions of falsification could be coupled with comparative theory testing to provide some general normative guidance. This is not to deny the value of SMF in providing meaningful reconstructions of historical events so that progress many he assessed or observed, nor is it intended to suggest that a series of very specific rules for conducting (as opposed to judging) research will be possible.

More generally, while we make reference to the historical roots and evolution of falsification ism by citing Popper and Lakatos respectively, it should be apparent that the intent was not to adopt the views of either of these philosophers wholesale - instead we build upon them in developing our own position. Ironically, in arguing that we are "instrumentalists," Anderson both notes that Popper was a "strident anti-instrumentalist" and in the same sentence mockingly characterizes Popper as our "hero". This effort to pigeonhole us and our views via "guilt by association" with Popper, "positivism" and now, "interpretivism", not only is riddled with the sort of inconsistencies Anderson himself notes, it also does little to encourage a meaningful dialogue. We do not assume that Anderson finds heros in and shares all the views of scholars such as Laudan, Feyerabend and Wittgenstein. His efforts to criticize our position would be better directed at the content of the arguments we present than at applying ill-fitting pejorative labels and reacting to the larger body work authored by philosophers we reference only in passing.

It is our position that a falsificationist orientation (in the very simple sense of continuing to subject theories to tests in which they could fail or have their weaknesses revealed) coupled with a commitment to selecting theories comparatively (i.e., preferring ones that provide the most complete yet parsimonious account of available data) can and should he the general methodology for generating scientific knowledge. Note that these principles do not assume that theories can be demonstrated to be either true or even unequivocally false, nor is there any inductive implication that the greater the number of tests a theory has survived the "better" it is. Moreover, the interpretation of data will change as theories evolve and it is conceivable that a theory might reasonably be discarded and later resurrected (perhaps in some revised form) when additional data for which it can account become available. All we suggest is that a process of ongoing testing, and a preference at any point in time for theories that provide a better explanation than their rivals offers the possibility of scientific progress. This is the best we can hope for.

With this broad statement of our position on the methodology for creating scientific knowledge in mind, we now turn to the practical issues raised by Peter and Olson. They question the adequacy of our view in providing normative criteria asking "How many attempts to refute a theory must be made to conclude that the theory is falsified? In comparative 'tests' of alternative theories, how much better must the empirical results be before a winner is identified? Who decides what constitutes a valid falsification test? What is to be concluded when some comparative results support one theory and some support the other? (this volume, p. 25)"

We offer several responses to these questions. First, no matter what the criterion, judgment will always play a role in choosing among theories. But, if individuals share the overall goal of progress in understanding/accounting for phenomena, then many disputes can be resolved and general guidelines are possible. As suggested in outlining our broad view, the number of theory tests per se says nothing about whether or not a theory should be abandoned. Further, theories typically are and should be abandoned on a comparative basis -- it is appropriate to abandon one theory when there is a superior alternative. Thus, theories may continue to be used even though some of their weaknesses have been exposed if no rival presents itself. In comparing theories that compete, we argue that the one that parsimoniously accounts for the greater number of phenomena (and not studies or data per se) should be preferred. No doubt there will be many instances in which no theory is clearly superior, and these are areas in which any verdict must await further research. For example, if two theories explain the same number of only partially overlapping phenomena, the limitations of both theories would be apparent and, ideally, further research would seek a broader theory than could encompass the phenomena explained by both of the previous theories. (An example of such a situation is reported in Tybout, Sternthal and Calder 1983.) As to who decides what constitutes a valid falsification test, from a normative perspective this should be other researchers who, irrespective of their own research program, share an overriding commitment to scientific progress as measured by explaining an ever increasing set of phenomena. Practically, judgment occurs via the review process, and sociological agendas, of course, may dominate this normative criterion.

In sum, we argue scientific knowledge is best served by continuously testing theories and comparatively selecting the ones that can best account for a set of phenomena at a point in time. There cannot and should not be hard and fast rules such as five tests are better than four, or tests that following traditional experimental procedures (i.e., random assignment to treatments, manipulation checks, process measures) are inherently superior to ones that do not observe these conventions. The adequacy of a test can only be known post hoc -_ good tests are ones that render rival explanations for the data implausible. Strategies such as increasing the number of tests and employing traditional experimental procedures only have value to the extent they serve this goal, not the reverse. (See Sternthal et al. 1987 for more on this topic.)

Falsificationism is Passe'

Finally, critics of our position are fond of characterizing falsificationism as so outre that only a backwards country bumpkin would mention this "f-word" in the same breath with current philosophy of science (Anderson this volume; Holbrook and O'Shaunghnessy 1988; Peter and Olson this volume). They assert that even the "advanced" physical sciences have abandoned falsificationism.

We suspect that much of this response stems from equating falsificationism with Popper's original formulation and has little to do with the brand of falsificationisin we advocate. Perhaps the term "falsificationism" carries so much excess baggage it would facilitate future communication to think of our view at a more operational level as the "empirical-comparative" approach. In any case, our views appear quite compatible with the positions of many leading scientists (e.g., Hawking 1988). Even Holbrook and O'Shaunghnessy (1988) see sufficient merit in a falsification orientation to claim that it is an integral part of the interpretivists' Hermeneutic Circle!

Critical Relativism is Descriptive Rather than Normative Methodology

Anderson chastises us for not heeding his contention that critical relativism is first and foremost a descriptive methodology and does not constitute a set of normative guidelines. Therefore, he reasons, it is inappropriate for us to argue that "interpretive knowledge implies critical relativistic methodology."

We acknowledge that Anderson has indeed stated that critical relativism is a descriptive enterprise. However, as noted by Siegel (1988), Anderson's efforts to disavow any normative claims for critical relativism are undermined by the very label critical relativism (an oxymoron?), his argument that Critical relativists are somehow more "hard-headed" than positivists in judging knowledge products, and his on-going promise to "cashout" the implications of critical relativism at the "workbench level." This cannot be a purely descriptive enterprise.

Further, our original framework sought to pair knowledge types with very general methodological approaches and not vice versa. Thus, aspects of Anderson's critical relativism that are descriptive may contribute to understanding of research as practiced under any approach. But normative features, such as the notion that knowledge outputs should be judged on a variety of non-empirical as well as empirical bases and the contention that multiple accounts for a phenomenon should be viewed relativistically rather than competitively, seem to reflect a methodological orientation compatible with the goals of interpretative knowledge as we have defined it. Of course, critical relativism does not outline specific steps for conducting a piece of research any more than does our falsificationist approach. What is lacking in critical relativism as a normative methodology at this point is that, although it specifies a range of considerations in judging knowledge products (e.g., a program's methodological, ontological, metaphysical and axiological commitments), and it tells us what not to do (e.g., don't judge on strictly empirical bases or comparatively), it stops short of telling us how to recognize a "good" interpretive knowledge product.

Critical Relativism and Data

Both Anderson and Peter and Olson complain that we accuse critical relativists of avoiding data when in reality they (critical relativists) "... recognize that empirical results can play an important role in generating social consensus about theories," but are "...much less impressed with empirical data and its role in science than are Calder and Tybout (Peter and Olson, this volume p.26)." Our point was not that critical relativists would refuse to consider data. Rather we were arguing that the possibility of appealing to non empirical factors in evaluating theories is more an illusion than a reality. How might one argue the merits of a methodology, ontology, axiology etc., if not by appealing to some form of data or empirical observation? We did not intend to suggest that critical relativists ignore data -- just the opposite. We suggest that they are no better or worse than empiricists in their reliance on data. The primary difference lies in whether the data under consideration are limited to controlled studies Or give greater emphasis to observations of naturally occurring events.

Unfortunately, as part of their case for the superiority of the critical relativists' approach over traditional empirical science, Peter and Olson call into question the validity of experimental data; stating, "...we know that well-trained researchers can construct empirical data and results to support or refute almost any theory without violating 'accepted standards' of research in the field (p.26)." As active empirical researchers ourselves, we can only imagine that such a statement was intended to be more provocative than literal. How could they know such a thing? Have they as researchers found desired results so easy to produce as to make them this cynical? Could their subjects be that much more cooperative and the reviewers of their papers that much more naive than the ones we encounter? Why are journal rejection rates so high? Is it because most researchers are poorly trained in the art of producing desired results or is it that reviewers are as cynical as Peter and Olson and reject research conforming to 'accepted standards' unless it also fits their personal/political sensitivities? And if empirical tests are flawed, does it follow that instead of attempting to improve them we should place greater reliance on more subjective means of choosing among theories? We can only hope that the Peter and Olson view of empirical work is not widely shared. It certainly does not fit our personal experience nor our view of the field.

Anderson's Illustrative Critique of Tybout, Sternthal and Calder (1983)

Finally, Anderson argues against traditional empirical science and for the broader range of research methods embraced under critical relativism on the grounds that the knowledge products of traditional empirical science have been, in the eyes of many, disappointing. To this end he focuses on a article in which Tybout et al. (1983) report four experiments examining an avail ability-valence explanation for multiple request techniques (i.e., foot-in-the-door and door-in- the- face). To borrow a phase from Anderson's chapter, "space limitations" do not a permit a detailed point by point response. However, we will react to several of the broad themes raised.

First, the study is presented as both an example of positivist research and psychological instrumentalism. As alluded to earlier, there would seem to be a fundamental contradiction in these labels in view of positivism's association with the verifiability principle and instrumentalist's reliance on constructs lacking any real world referent. We would prefer not to use either label and consider ourselves simply to conduct TSE studies.

Second, Anderson charges that we have "altered" Tversky and Kahneman's (1973) availability hypothesis. We can only agree and suggest that such action is necessary and desirable in the process of broadening the scope of a theory. Tversky and Kahneman focused on judgments of the frequency of event occurrence. The availability or ease with which information related to events could be retrieved was sufficient to make predictions in this context. By contrast, we examined compliance behaviors. Here, predictions required anticipating both the availability information and the valence or favorableness of that information. Thus, part of our intended contribution was extending the basic availability notion of Tversky and Kahneman. It is difficult to see why that should be criticized per se.

Third, because the constructs we discuss are availability of information in memory and judgment, Anderson draws upon a recent review of the memory-judgment literature by Hastie and Park (1986) in an effort to demonstrate that there may be multiple explanations for our findings. Specifically, he suggests that it is unclear whether on-line or memory based processing is responsible for the results we predict and observe. The general spirit of this effort is one we wholeheartedly endorse. Progress is best made by generating and ruling out alternative explanations and it is always desirable to push extant theorizing toward more precise predictions regarding the underlying process.

However, several caveats are relevant to Anderson's particular, and in context, peculiar, efforts along these lines. First, any viable rival explanation must account for at least as much data as the advocated theory. Anderson only alludes to an explanation for outcomes in one of the four experiments we report and offers no interpretation for the larger multiple request literature that we review and explain. Because the multiple request outcomes our theorizing accounts for span ones involving delay (and thus are more prone to memory-based judgment) and ones involving contiguous requests (which although favoring on-line availability effects would still require accessing long-term memory to assign a favorable or unfavorable valence to the available behavior), rival explanations based on the memory based versus on-line judgments are not highly plausible. But, had Anderson been able to generate a viable rival explanation for our results we would view it as signaling a direction for future research and progress, both of which would be welcome. We fully expect that our explanation will be modified/ex tended (as we did with Tversky and Kahneman's hypothesis) or discarded as new theorizing and data become available.

More generally, after labeling us as "instrumentalists," Anderson charges that "instrumentalists' lack of concern for the details of process, their excessive emphasis on prediction, and their casual attitude toward the meaning (emphasis original) of the key concepts mentioned in their theories has led 'positivistis' and interpretivists alike to turn away from this approach" (p. 16). Although we may share with instrumentalists the view that theoretical constructs are unobservable, if Anderson has accurately depicted the instrumentalists' position on the importance of the meaning of constructs (and we suspect he has not), then it is most certainly not our view. The very essence of our position on theory testing is one of ruling out rival explanations, in other words, triangulating operationalizations to arrive at a single plausible interpretation for the constructs underlying a phenomenon. It is difficult to imagine how this can be construed as a "casual" attitude toward the meaning of key constructs. Moreover, we know of no alternative to examining the correspondence between data and theory as a basis for ruling out rival explanations. To suggest that theoretical constructs and processes can be directly observed, as Anderson seems to imply when espousing the virtues of ethnomethological approaches (p. 21), is to dispute the basic notion that theories are abstract and therefore generalizable. Could this be his intention?

Finally, Anderson speculates about how an ethnomethodo lo gist might view the multiple request situation. He summarizes this discussion with the following observation; " is the different (metaphysical) conceptions of man that lay at the heart of the distinctions between ethnomethodology and psychological instrumentalism. For the latter, man is often a judgmental dope whose verbal and motor behavior result from the operation of an autonomous central nervous system. On the other hand, while ethnomethodologists see man performing his mundane everyday activities in a largely unreflective fashion, there is always the possibility of choice (p.21). " Stated more graphically, the psychological instrumentalist bears more than a passing resemblance to the manipulative mad scientist of horror film fame and the ethnomethologist is someone you wouldn't mind having as a next door neighbor. Anderson concludes by suggesting that, as consumer researchers, we might do well to select our approach on the basis of which model (psychological instrumentalism or ethnomethodology) we would like to have applied to ourselves.

In contrast to Anderson's focus on the differences between his view of psychological instrumentalism and ethnomethology (which undeniably exist), we are impressed with what these approaches have in common. For example, Anderson's ethnomethodological interpretations of compliance with multiple request strategies were remarkably similar to the self-perception and bargaining -concession explanations offered in the psychology literature. (And it should be recalled that these explanations were by themselves inadequate to account for the total pattern of findings in the literature, thus motivating the Tybout et al. 1983 research.) Further, the contention that the basic premises of cognitive psychology necessarily cast subjects in the pejoratively-termed role of "judgmental dopes" is downright silly. The observation that many cognitive responses are so well learned as to require no conscious attention (i.e., they are "automatic") is better viewed as evidence of an adaptive human organism or a "judicious processing." Moreover, psychologists devote considerable attention to exploring the conditions under which automatic processing will be interrupted and conscious attention devoted to choosing among alternative courses of action. Thus, cognitive psychologists address the very same issues that Anderson attributes to ethnomethologists and it would seem that they are if anything more concerned with probing the underlying process. Finally, we can not hope to progress in our scientific understanding of the world if we choose explanations on the basis of the extent to which they flatter our self-images or conform to our intuitions.

Despite the foregoing disagreements with Anderson's comments on Tybout et al. (1983) in particular and cognitive psychology in general, we end our response on a note of harmony. We share with Anderson a desire to push extant theories toward greater specificity and clarity and we applaud his effort to do so by attempting to develop rival explanations for a phenomenon. We hope this type of dialogue will continue but suggest it would be better served by avoiding pejorative characterizations of alternative approaches.

In sum, the foregoing discussion reveals that Anderson's and Peter and Olson's criticisms largely reflect misrepresentations and misunderstandings of our views and as such cannot support their conclusion that they discredit our framework. With this established, we now turn to some of the implications of our framework for the qualitative and interpretive approaches.

Before continuing, it should be noted that although the title of this book suggests the focus is on the interpretative approach, several of the chapters report research that, within our framework, seem more reflective of the qualitative approach. To clarify this distinction we now turn to a discussion of the nature of qualitative research.


The TSE approach rejects the relativist's critique and assigns a central role to challenging theory with data and little importance to the source of theory. The qualitative approach is exactly opposite in this respect. It seeks to capture the explicit or implicit theories (ideas) a group of consumers have about their own consumption behavior. It takes these theories at face value and adopts the attitude that consumers have, that these theories are naturally right (see Calder, 1977).

Even if one could show that consumers' theories might be wrong from a scientific or interpretive point of view, this would miss the point of the qualitative approach. The goal is to represent how the world is seen by the consumer. The researcher may or may not accomplish this goal. But, if the goal is met, there is no question of challenging the theory.

It is in this vein that several of the widely cited dictates of Lincoln and Guba (1985, p. 37) make imminent sense:

* Realities are multiple, constructed, and holistic.

* Knower and known are interactive, inseparable

* Only time- and context bound working hypotheses (ideographic statements) are possible.

These reflect the very nature of qualitative research. (But note that this hardly implies that the contrary assumptions made by the TSE approach are invalid.)

As already noted, the qualitative approach eventually comes down to the dictum that what people think to be true will ultimately affect their behavior. This may not actually be the best explanation. Perhaps a TSE or interpretive approach can do better in a given area. But it certainly is an important explanation of consumer behavior to consider and this is affirmed by the extensive use of focus groups and other qualitative methods in marketing practice.

Let us return to the point alluded to above that any particular qualitative account can be wrong. Not, as noted, in a scientific sense, but simply in terms of errors in the way the qualitative account is constructed. In a recent article in the anthropological literature, Heider (1988) points out a number of potential errors that can be made, such as looking at different subcultures or the same cultures at different times or the different orientations among ethnographers. And in the present volume Wallendorf and Belk make a number of recommendations aimed at guarding against such errors. Prolonged engagement, rapport with consumers, triangulation across researchers, researcher self-analysis all are held up as desirable safeguards.

Such safeguards are clearly reasonable. In looking at recent qualitative studies as represented by this volume, however, we are struck by a different, though related issue. Yes, it is important that qualitative studies develop better safeguards against error. It is equally important, however, that qualitative studies develop conclusions strong enough to be checked for error. Heider (1988, p. 75) provides a good example. Ethnographers who spend longer time in the field are apparently more likely to find that deaths are attributed to witchcraft. One can immediately begin to consider whether time in the field is a source of error in the conclusion of some researchers that witchcraft attributions are not made in a culture. Our point is that this depends on the researcher having in fact drawn a conclusion for or against witchcraft attribution. As Heider puts it, the presence or absence of witchcraft is "a truly determinable fact" (p. 75). We need such determinable conclusions in consumer research in order to begin to assess the possibility of error.

A qualitative analysis by Sherry and McGrath in the present volume provides a case in point. They provide a thick ethnographic description of two gift stores. The possibility or error is amply acknowledged: the study is said to "enfranchise speculation within obvious limits" (p. 149). But what of the conclusion?

The two strongest and clearest conclusions (or propositions deserving more systematic investigation," p. 161) drawn by Sherry and McGrath are that a sense of place is important for the retail stores and that gift giving is the work of women. On the one hand these conclusions do fit the ethnographic description. On the other hand, they fit so loosely and generally that it is difficult to see how the ethnography has contributed to a richer understanding of how the consumer perceives the retail place and takes it into account or how women see their role in shopping. As specific as the authors get is the conclusion that some female consumers are "driven by the principle of shop 'til you drop.' What this means qualitatively from the view of the consumer, however, is not developed as a conclusion of the research.

Another case of extensive description but weak conclusions is Hirschman and LaBarbera's (this volume) analysis of the meaning of Christmas. The conclusion is that Christmas is multidimensional in meaning: "both happy and sad, ingenious and cynical, spiritual and crass, selfish and altruistic..." (p. 145). Again, the conclusions do not seem to capture and communicate what the idea of Christmas is to a group of consumers from their perspective.

Our point is that the richness of the qualitative approach is not being reflected in the conclusions of the research. It is true that if the conclusions are weak or general enough they are not likely to be wrong. But with stronger, more definitive conclusions we could begin to explore whether they are right or wrong.

Our suspicion is that part of the reluctance to draw strong conclusions in qualitative studies of consumer behavior stems from a misconception perpetuated by Lincoln and Guba (1985, p. 37). Two more of their dictates are:

* All entities are in a state of mutual simultaneous shaping, so that it is impossible to distinguish causes form effects.

* Inquiry is value bound.

If taken literally the first of these points would seem to almost prohibit conclusions from qualitative research. Nothing can be linked to or used to explain anything else. Yet the whole point of qualitative research is to show how the ideas of consumers shape their thinking and behavior. Thick descriptions that capture consumer experience are necessary, indeed, at the heart of qualitative methodology. How else, to experience the consumer's world?

But description per se is not enough. The researcher has to draw conclusions that reveal chains of logic and point up perceptions that shape behavior. There is nothing in this that denies the nature of qualitative research.

A final point regarding the conclusions of qualitative research. We detect a tendency to substitute interpretation and even value judgments for true qualitative conclusions. For instance, in the Sherry and McGrath conclusion regarding "shop 'til you drop" the authors go on to label these women as "shop-aholics" and call for an understanding of their "compulsions."

Now it is very doubtful that women see themselves in this light; or at least we see nothing in the thick description to suggest this. It may well be that from some other, interpretive perspective the notion of compulsion is appropriate. This is not, however, faithful to the qualitative approach.

We can of course anticipate a response that it is not possible in practice to avoid interpretation in providing an ethnographic description. We acknowledge that in a sense this may be true. But it is still useful to attempt in principle to minimize nonconsumer interpretations in qualitative accounts.

At the very least it seems to us inconsistent to in fact purposely exceed the limits of thick description in order to draw conclusions. Again the Sherry and McGrath analysis provides a good illustration of our point. In discussing their sense of place conclusion, the authors go on to note that this may seem to be only the store "atmosphere" effect that has been widely discussed in the marketing literature. They claim however that their study suggests a more "higher order rendering of atmospherics" (p. 162). Yet to develop this they go to a discussion of "pathetecture" rooted in an interpretive literature far removed from the world of the consumer.

It may well be impossible not to have some interpretation creep into qualitative accounts. Clearly it is possible to avoid deliberately mixing the two in such a way as to confuse the ways conclusions are being reached.

Moreover, it is certainly possible to avoid going all the way to pure value judgments in order to reach qualitative conclusions, even though Lincoln and Guba may seem to justify this. In this volume Belk uses content analysis of cartoons to identify the role of materialism in the modem Christmas. As with the Sherry and McGrath article, the description is interesting. But the conclusions are especially puzzling: seems to have fallen on the simple and humorous cartoon format to tell us that there is something unsettling with the modem American Christmas. Perhaps we should take such cartoon messages seriously. (Belk, p. 132)

Unsettling to whom?


New approaches to consumer research offer the real possibility of bringing fresh creativity to the field. However, we worry that this creativity may be masked by expressions of personal sentiment. Even worse, such expressions may actually masquerade as research creativity.

This expressiveness seems to range from the relatively innocuous to the somewhat bizarre. Two instances found in the present volume are illustrative. Consider first Hirschman and LaBarbera's analysis of the meaning of Christmas. We have already contended that their conclusions fail to do justice to their qualitative approach. It must he added that they go beyond these conclusions to express an appreciation of Christmas as an individual, personal experience.

Consumers make of Christmas what they can; what they will; what they wish. The true meaning of Christmas lies within each of us; and for each of us, it is a unique truth. (p. 145)

What this truth is and how its explication can contribute to an understanding of consumer behavior is only further obscured by this sort of poetic statement. What we have is an expression of personal sentiment. There is no creative insight or even inspiration that can be of use in the research process. 'Mere is a danger of style before substance.

Ile Holbrook, Bell and Grayson's paper in this volume expressly argues for a broader view of interpretation, one that incorporates artistic expression at its roots. Thus the authors present not only literary criticism but a personal experiment in "irony" as well. They describe a study that was first submitted to the Journal of Consumer Research and reviewed by one of us (BIC). Ile study is a personality impression formation study in which subjects make inferences based on a short story that describes consumption behavior. The study is motivated as an empirical attempt to test Holbrook and Grayson's (1987) interpretive work.

This study was rejected by the journal. Although not presuming to speak for the editor, it seems clear to us that most TSE researchers would regard this study as making a very limited contribution. It's main weakness is that the theory being tested is very limited. That subjects do form impressions from consumption information has long since been established. The impression formation literature has become quite large, with a number of theoretical issues emerging that require empirical testing. The Holbrook et al. study fails to make contact with any of these issues. The study would perhaps have made a contribution fifteen years or more ago.

Holbrook, Bell, and Grayson contend that they are submitting their interpretive ideas to empirical testing as suggested by Calder and Tybout (1987). They fail to realize, however, that their theory (that people infer personality from behavior) carries over nothing from their interpretive work. It is hardly an example of inspiration. And, as we have said, the study does not even attempt to connect with existing theory. The mere fact that the study uses a simulated short story has no hearing on the rigor of the theory test. No theoretical variable is operationalized through the story.

The authors wish to argue though that either their study supports their interpretive work (and since the study carries almost nothing over from this work it is unclear how this could be the case) or (and they prefer this) that the study is:

... a piece of sustained irony that casts self-critical doubt on the use of falsificationist procedures to clarify the meanings of artworks and that thereby reaffirms the potential validity of interpretivism (p. 39).

The logic appears to be as follows: because the theory in this study is sterile, it follows that TSE theory is always inferior to interpretive work--"we freely acknowledge the inevitable limitations and weaknesses in the empirical enterprise" (p. 40). Obviously, the logic here is tortured. Moreover, it fails to take into account that it was Holbrook et al. who set up the theory test that .1 proves" the inferiority of the TSE approach to their interpretive work.

Beyond the inadequacy of the Holbrook et al. logic, there is something more troubling. It is the idea that one's personal intentions in submitting a paper somehow matter and that reviewers are somehow obligated to read between the lines to detect larger meanings (e.g., any intended irony). It seems to us that this turns the entire research enterprise into an exercise in expression.


We have not attempted a micro-level review of individual research programs since there seems to be a consensus that emerging approaches in consumer research are not as yet well enough developed to warrant this and might even be hampered by it. Instead we have focused on three, more macro impediments to the developments of new approaches as reflected in this volume and recent published articles.

We hope that, taken in conjunction with Hunt's critique, our comments help to expose the vacuousness of the critical relativists' attack on traditional scientific empirical research. This research does not reduce to be the same as any other research approach. It is a specific approach that must be debated on its own terms as we have tried to do (see Sternthal et al. 1987). Misguided attempts to undermine the special concerns of this approach can only endanger true methodological pluralism.

We also hope to have made it clear that methodological pluralism is a goal that both TSE researchers and qualitative and interpretive researchers can support. At this point we need to focus on impediments to the development of qualitative and interpretive approaches. This can only be done through constructive criticism. In this spirit we call for an effort to reach stronger, more truly qualitative conclusions in qualitative research. It is our belief that questions of methodological error can be more readily addressed if this is done.

Finally, we applaud creativity in interpretive work and research efforts, in general. However, we caution that creativity is not synonomous with self-expression. What is needed is creativity in advancing the research process, and thus our understanding of world, from each of the three perspectives.


Anderson, Paul F. (1983), "Marketing, Science Progress and Scientific Method," Journal of Marketing, 47, 18-31.

Anderson, Paul F. (1986), "On Method in Consumer Research: A Critical Relativist Perspective," Journal of Consumer Research, 13, 155-173.

Calder, Bobby J. (1977), "Focus Groups and the Nature of Qualitative Marketing Research." Journal of Consumer Research, 14, 353-364.

Calder, Bobby J., Lynn W. Phillips and Alice M. Tybout (1981), "Designing Research for Applications," Journal of Consumer Research, 8, 197-207.

Calder, Bobby J. and Alice M. Tybout (1987), "What Consumer Research Is Journal of Consumer Research, 14, 136-140.

Hastie, Reid and Bernadette Park (1986), 'The Relationship Between Memory and Judgement Depends on Whether the Judgement Task is Memory-Based or On-Line," Psychological Review, 93, 258268.

Hawking, Stephen (1988), A Brief History of Time: From the Big Bang to Black Holes, Bantam Books: NY.

Heider, Karl G. (1988), "Me Rashomon Effect: When Ethnographers Disagree," American Anthropologist, 90, 73-81.

Lincoln, Yvonna S. & Egon G. Guba (1985), Naturalistic Inquiry, Beverly Hills: Sage.

Holbrook, Morris B. and Mark W. Grayson (1986), "The Semiology of Cinematic Consumption: Symbolic Behavior in Out of Africa," Journal of Consumer Research, 13, 374-381.

Holbrook, Morris B. and John O'Shaughnessy (1988), "On the Scientific Status of Consumer Research and the Need for an Interpretive Approach to Studying Consumption Behavior," Journal of Consumer Research, initial draft of paper that is forthcoming December.

Seigel, Harvey (1988), "Relativism for Consumer Research? (Comments on Anderson)," Journal of Consumer Research, 15, 129-132.

Sternthal, Brian, Alice M. Tybout and Bobby J. Calder (1987), "Confirmatory versus Comparative Approaches to Judging Theory Tests," Journal of Consumer Research, 14, 114-125.

Tversky, Amos and Daniel Kahneman (1973), "Availability: A Heuristic for Judging Frequency and Probability," Cognitive Psychology, 5, 207-232.

Tybout, Alice M., Brian Sternthal and Bobby J. Calder (1983), "Information Availability as a Determinant of Multiple Request Effectiveness, " Journal of Marketing Research, 20, 280-290.



Bobby J. Calder, Northwestern University
Alice M. Tybout, Northwestern University


SV - Interpretive Consumer Research | 1989

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