Paul F. Anderson (1989) ,"", in SV - Interpretive Consumer Research, eds. Elizabeth C. Hirschman, Provo, UT : Association for Consumer Research, Pages: 10-23.
[The author would like to thank Elizabeth Hirschman, Jerry Olson, J. Paul Peter, John Sherry, Harish Sujan and Melanie Wallendorf for their very helpful comments on various portions of earlier drafts of this paper.] INTRODUCTION The relationship between relativism (especially critical relativism) and methodologies that fall under the rubric of interpretivism has always been somewhat opaque in our discipline. Unfortunately, the waters have recently been muddied further by Calder and Tybout (1987). One objective of this paper is to clarify some of the misunderstandings created by Calder and Tybout's view of critical relativism. A second objective is to begin the process of explicating the reasons why some researchers in social science and consumer research have abandoned
[The author would like to thank Elizabeth Hirschman, Jerry Olson, J. Paul Peter, John Sherry, Harish Sujan and Melanie Wallendorf for their very helpful comments on various portions of earlier drafts of this paper.]
The relationship between relativism (especially critical relativism) and methodologies that fall under the rubric of interpretivism has always been somewhat opaque in our discipline. Unfortunately, the waters have recently been muddied further by Calder and Tybout (1987). One objective of this paper is to clarify some of the misunderstandings created by Calder and Tybout's view of critical relativism. A second objective is to begin the process of explicating the reasons why some researchers in social science and consumer research have abandoned"positivistic" approaches in favor of interpretivism. It is not, however, a general defense of interpretivism.
ON SPECIOUS CLASSIFICATIONS
Calder and Tybout begin their article by creating a classification system that divides the knowledge produced by consumer research into three categories: 1.) the everyday, 2.) the scientific, and 3.) the interpretive. Here they have dredged up a philosophical controversy with a history reaching back more than two millennia: the so-called demarcation problem. As I have noted elsewhere (Anderson 1983), the inability of science studies researchers to agree on the existence of a unique scientific method suggests that we currently have no universally applicable criterion by which we can demarcate scientific knowledge from any other kind of knowledge (Laudan 1983a). As Laudan has stated, "The fact that 2,400 years of searching for a demarcation criterion has left us empty-handed raises a presumption that the object of the quest is non-existent" (1980, p. 275). [As suggested by the philosopher Richard Rorty (1979), this does not mean that epistemology [or the broader field of science studies] is the ultimate "foundational" discipline that "legitimizes or grounds the others" (p. 6). Nor does it mean that scientists in a substantive field (like Pierre Duhem) cannot make contributions to epistemology. I am simply suggesting that when philosophy of science issues are at stake, it seems reasonable to consult the work of professionals who have devoted their careers to such matters. Whether we accept or reject their (often conflicting) positions is another matter entirely.]
Unfortunately this is often thought to imply that all knowledge claims are on an equal epistemic footing (Hunt 1984). Of course, nothing could be further from the truth. Indeed, very little follows from the fact that philosophers have been unable to come up with a universal demarcation criterion. The fact that all of the proffered alternatives have crumbled under the weight of criticism is nothing more than an empirical statement whose epistemological import is of minimal consequence. This can be seen in the diversity of philosophers who disagree on almost everything else-but are as one in their opposition to demarcationism. Thus Laudan (a rationalist, antirelativist and anti-realist), Rosenberg (a naturalist, anti -relativist, and realist), and Feyerabend (an epistemological anarchist, relativist, and "flippant Dadaist") all agree that no one has yet to produce a defensible criterion of demarcation. Moreover, as I tried to show in Anderson (1986), the lack of such a criterion is no hindrance in critically evaluating the knowledge claims of alternative research programs. Thus, the search for unique characteristics that mark off the scientific from the non-scientific is a chimerical quest that (like the medieval crusades) is very likely to lead to failure.
Regrettably, Calder and Tybout have associated themselves with one of the least defensible of the demarcation criteria: Popperian falsificationism (Popper 1959). On this view, a discipline is scientific if it is willing to make predictions that can be refuted by empirical data. To quote Laudan (1983b) again, this view
Has the untoward consequence of countenancing as "scientific" every crank claim which makes ascertainably false assertions. Thus, if I subscribe to some aberrant theology which says the world will end on January 4th in the year 2000, 1 can establish my Popperian scientific bona fides by saying that if the world endures beyond that date, then I was mistaken! (p. 23).
The problem with Popper's demarcation criterion is that it can be construed in such a way that it excludes disciplines taught as science in our major universities while at the same time it includes fields that have yet to attain the status of what I have elsewhere called science2-the definition of science by societal consensus (Anderson 1983). Thus, Popper's (1957) notorious claim that evolutionary theory is not testable must call into question the scientific status of most, if not all, of modem biology. Similarly, if 'The key features of scientific knowledge are that there have been empirical attempts to refute a theory and that the theory has performed better than any available competitors" (Calder and Tybout 1987, p. 137), we are left with the problematic case of parapsychology. The practitioners of this field will claim that they have met and even exceeded Calder and Tybout's criteria. Indeed, as two outside observers have noted, "It seems likely that the best of modem parapsychology comprises some of the most rigorously controlled and methodologically sophisticated work in the sciences" (Collins and Pinch 1979, pp. 243-44). [Collins and Pinch are sociologists of science who have done extensive empirical research on parapsychology. They have no vested interest in its scientific legitimacy; and have, in fact, observed and publicly reported cases of fraud in so-called .. paranormal metal bending" (Collins and Pinch 1982).] (In fact the field tries to maintain such standards because of society's unwillingness to grant it epistemic authority! ) [Of course, this does not suggest that society should recognize parapsychology as science. My point is that Calder and Tybout's criteria are not strong enough to rule parapsychology out of court on their own conception of scientific knowledge.] They go on to state that,
Although a group of scientists have dedicated a considerable portion of their lives to the attempt to discredit psi [e.g., telepathy, clairvoyance, precognition, etc.] .... they have not succeeded in revealing any universally acceptable criteria to distinguish parapsychology from science (Collins and Pinch, 1979, p. 250).
Thus, if Calder and Tybout wish to maintain the integrity of their classification system, they must do what has eluded philosophers since the time of Parmenides: develop a demarcation criterion that divides knowledge into mutually exclusive categories.
ON SOME HONEST MISUNDERSTANDINGS
Calder and Tybout argue that sophisticated falsificationism should be the methodology for generating "scientific" knowledge in consumer behavior. In so doing, they are asking us to adopt a philosophy of science that has long since been abandoned by the broader science studies community. Of course, rejection by scholars in this field does not, by itself, constitute sufficient grounds for its dismissal in consumer research. If falsificationism 'is to be repudiated, it must be because "good" reasons have been offered for its inadequacy. (Indeed, some of these reasons have already appeared in the marketing and consumer behavior literature.) However, it would appear that Calder and Tybout do not find these arguments compelling. They apparently believe that the only arrow in the relativist's quiver is the charge that all scientific data are fallible (Calder and Tybout 1987, p. 138). This is indeed a point made by relativists, but if it were our only concern with falsificationism, our position would reduce to an empty skepticism. Unfortunately, the problems with falsificationism run far deeper than this.
First, it should be clear that falsificationism rests on the very same inductivism that Calder and Tybout find so objectionable (Calder, Phillips and Tybout 1981; Calder and Tybout 1987). In the Popperian system, a theory is said to be .. corroborated" (tentatively accepted) if it has survived repeated and determined efforts at falsification. However, it should be clear that Popper has simply substituted accumulated "failed falsifications" for accumulated verifications. He is thus making an inductive leap from a finite number of experiments to the "corroboration" of a theory with alleged universal applicability. As I have noted elsewhere, this mode of inference runs headlong into the "problem of induction" (Anderson 1983, p. 19); and, as Calder and Tybout have noted, induction is not a deductively valid form of inference.
Second, falsificationism also falls victim to the Duhem (1906, 1954) thesis. Since all theory tests depend on other theories concerning initial conditions, measuring devices and auxiliary assumptions--any alleged falsification can always be "deflected by assuming that something else in the maze of assumptions and premises caused the result" (Anderson 1983, p. 21). Moreover, since all experiments are inherently "open systems" (Pickering 1981, 1984), it is rarely possible to deter-mine if a study is actually a rigorous test of a hypothesis (in the sense that we can determine that the theory actually had a genuine chance at failing).
Third, Calder and Tybout claim that they are proposing "a methodology of sophisticated falsificationism" (p. 138) derived from the works of Popper (1959) and Lakatos (1970). However, in Popper's 1959 book [actually published in 1934] he expounds a view that Lakatos (1978) criticizes as "naive methodological falsificationism" (p. 108n). Moreover, Calder and Tybout do not take note of the fact that Lakatos's "sophisticated falsificationism" was never intended to give normative guidance to practicing scientists. Lakatos's "methodology of scientific research programs" was devised to give historians of science a means of creating "rational reconstructions" of actual historical episodes (Lakatos 1970, 1978). A rational reconstruction is a historical narrative that "recreates" the actual events so as to produce "some characteristic pattern of rational growth of scientific knowledge" (Lakatos 1978, p. 118). As Lakatos (1971) himself put it:
I, of course, do not prescribe to the individual scientist what to try to do in a situation characterized by two rival progressive research programs ... Whatever they have done, I can judge: I can say whether they have made progress or not. But I cannot advise them--and do not wish to advise them--about exactly what to worry and about in which direction they should seek progress (p. 178, emphasis in original).
Thus, Lakatos counsels that in any reconstruction of the work of Niels Bohr "the historian, describing with hindsight the Bohrian program, should include electron spin in it [even if Bohr may never have thought of electron spin], since electron spin fits naturally in the original outline of the program" (1978, p. 119). Lakatos took this rather idiosyncratic approach to philosophy of science because he realized that it is only "with long hindsight" that we can judge one program to be superior to another (Lakatos 1970, p. 173, emphasis in original). This is also why his sophisticated falsificationism can provide no rules for the contemporary scientist. The history of science is replete with examples of "degenerating research programs" that have staged spectacularly successful comebacks (Lakatos 1978; Chalmers 1982). Thus he can say that, "One may rationally stick to a degenerating program until it is overtaken by a rival and even after" (Lakatos 1978, p. 117n, emphasis in original). However, since "one can be "wise" only after the event" (Lakatos 1978, p. 113), one never knows when it is time to jump ship. [Here I am not claiming veridical exegetical powers when it comes to the work of Popper and Lakatos. I prefer to simply present their own words (or criticisms that are well documented in the literature), and allow the reader to draw his or her own conclusions.]
Finally, falsificationism is suspect because it fails to accord with either the history of scientific advance or the empirical study of contemporary science. As I have noted elsewhere, heliocentricism, oxygen theory, natural selection, relativity theory, continental drift, etc., are all examples of "successful" theories that were at one time or another "falsified" (Anderson 1983). More importantly, empirical study of the practice of contemporary science also shows that falsificationism does not accurately describe scientific method in the supposedly "advanced" natural sciences (see, for example, Collins 1975, 1981; Gilbert and Mulkay 1984; Knorr-Cetina 1981; Latour 1987; Latour and Woolgar 1979; Law and Williams 1982; Pickering 1981, 1984; Pinch 1980, 1982, 1986).
Of course, the "falsification" of theories that are now considered to be successful could be patched up with the argument that "Researchers may make some effort to protect a new theory or to reserve judgment because of the possibility of erroneous interpretation of data" (Calder and Tybout 1987, p. 138). Unfortunately, this view of Lakatos's argument runs into the same difficulty mentioned above. There are no guidelines available to determine how long we should protect a theory, or when anomalies or "falsifications" imply that it is time for a change of research programs.
Indeed, it is ironic that Calder and Tybout (1987) charge relativists with attempting to "escape from data" (p. 138), when much of the evidence for relativism is based on empirical data. In this paper and in two others (Anderson 1983, 1986), 1 have cited numerous empirical studies that support a relativistic construal of scientific practice. Moreover in Anderson (1986) 1 demonstrated that four empirically -based approaches to consumer behavior are unable to resolve their differences despite their alleged commitment to adjudication by data.
Calder and Tybout go on to suggest that relativists see scientific knowledge arising, not out of consensus about data, but out of consensus per se. On their view, if scientists do not attempt to persuade each other on the basis of data, there is nothing left to use as a tool of persuasion. There are at least three problems here. As noted above, it is patently false to suggest that relativists retreat from data. I attempted to make this as clear as possible when I stated that "Critical relativists do not eschew empirical testing" (Anderson 1986, p. 156). (This includes both quantitative and qualitative tests.) Second, I did my best in Anderson (1986) to demonstrate that commitment to an encapsulated research program in consumer behavior involves more than a reliance on empirical evidence. Indeed, the whole point of my Exhibit was to show that data are not always sufficient to adjudicate among competing theories or research programs.
Third, numerous sociological studies of ongoing controversies in natural science have shown that scientific debates are not readily "closed down" by simple appeals to empirical evidence. If Calder and Tybout wish to maintain their "data uber alles" position, they must show that these studies are all somehow tragically flawed. For example, they must explain why Dr. Joseph Weber felt that he was "out marketed" [Personal communication from Harry M. Collins, October 30, 1982.] in his attempts to persuade the physics community that he had detected gravitational radiation in the late 1960's (Collins 1975, 1981). Similarly, they must explain why in 20 years no one has attempted to replicate Professor Raymond Davis's "anomalous" finding that the sun produces less than a third of the neutrinos predicted by theory (Pinch 1980, 1986; Babcall 1987). [The recent fortuitous explosion of Supernova 1987a may provide evidence that will be sufficient to bring closure to the solar neutrino debate (Bahcall, Dar and Piran 1987). However, the leading expert in the sociology of this controversy has expressed serious reservations about this eventuality (Pinch 1987).] Finally, they would have to deconstruct Pickering's (1981) study of the search for free quarks in which he concludes that "scientific communities tend to reject data that conflicts with group commitments and, obversely, to adjust their experimental techniques and methods to "tune in" on phenomena consistent with those commitments" (p. 236, emphasis added). Numerous other studies could be (and have been) cited (Anderson 1983, 1986); however, the main point has been made. One of the fundamental underpinnings of critical epistemic relativism is empirical, and any critique of its tenets must show that this empirical base is in some way Suspect.
Unfortunately, Calder and Tybout's failure to acknowledge the empirical basis of critical relativism is not their only misunderstanding of my work. On page 138 they declare that "Interpretive knowledge implies Critical relativistic methodology" (Calder and Tybout 1987). There are two very serious problems with this view. ne first is that I took great pains in Anderson (1986) to deny any necessary linkage between critical relativism and interpretivism. Indeed, in 1986 a leading proponent of "interpretive" or humanistic methodology put it thusly:
Though relativism per se does not constitute an ontology or a methodology, the issues it raises about the socially constructed and context-bound nature of human knowledge have generated consideration of various philosophical traditions and methodological avenues that earlier would have been viewed as unacceptable within the boundaries of marketing science (Hirschman 1986, p. 237).
Hirschman's insightful recognition that critical relativism is not a scientific methodology brings us to the second major problem with Calder and Tybout's exegesis of my position on the relationship between relativism and method. As I noted in my article, "critical relativism is first and foremost a descriptive enterprise" (Anderson 1986, p. 157), and descriptions clearly do not constitute a set of normative guidelines. Since statements of "ought" cannot be deductively derived from statements of what "is", critical relativism underdetermines methodology (Anderson 1986). That is to say, two committed relativists can (and frequently do) disagree on the normative implications of their preferred philosophy of science.
Critical relativism is a descriptive philosophy of science with potential implications "for workbench'-level issues in consumer research" (Anderson 1986, p. 169). In my article I tried to suggest a number of specific methodological topics and areas where critical relativism might be salutary. Currently work is under way that will attempt to deliver on this promissory note. Ironically, Calder and Tybout recognize that I have yet to cash out the methodological implications of my position. They state that, "Although Anderson (1986) provides a conceptual framework for critical relativism, specific criteria for critical relativism as a methodology are yet to be presented" (p. 139). If this, then, is the case, how can they know that interpretivism implies a critical relativistic methodology?
ON APPEAL TO A SOCIALLY SANCTIONED INSTITUTION
Calder and Tybout state that "scientific knowledge implies sophisticated falsificationist methodology" (p. 137) and suggest that alternative ways of knowing (while legitimate) do not measure up to "scientific" standards. Of course, in western societies we are all enculturated with the belief that science occupies the highest rung on the ladder leading to wisdom and insight (e.g., Gieryn 1987). By relegating "everyday" [While Calder and Tybout (1987) note that "anthropology ... includes research aimed at everyday knowledge and research seeking scientific knowledge" (p. 138n), they do not mention ethnomethodology--a field whose sole purpose is the "scientific" and empirical study of everyday knowledge (Garfinkel 1967).] and "interpretive" knowledge to a "legitimate", but non-competing status with science, they are making an appeal to a shared cultural belief that is itself nothing more than a subset of everyday ("unscientific") knowledge.
This becomes clear in their characterization of "interprefivism". Among other things we are told that, "The hallmark [of interpretive research] is the application of a given conceptualization, or way of viewing, to consumer behavior (p. 138). We are also warned that, "because [interpretive data] may be used selectively and multiple interpretations of them may coexist, there is no intention of comparing interpretations in order to choose among them (p. 139, emphasis in original). Moreover, interpretive researchers make "no pretense of searching for refuting evidence or competing explanations for the same data" (p. 139). Worse yet, interpretive "insight is subjective and relative to a particular time, setting, and group of researchers... [where] empirical data do not play a self-correcting role" (p. 139). Finally, "The consensus of [interpretive] researchers may result more from dogmatic acceptance than critical debate and agreement... [thus] such conceptualizations should not he equated with scientific knowledge" (p. 139).
Since it is not my intention to argue for or to defend the many approaches that fall under the rubric of "interpretivism", I shall leave a detailed critique of these points to others more qualified than myself. Suffice it to say that, when applied to the majority of work done under the banner of interpretivism, all of Calder and Tybout's claims are patently false. [In this regard, some useful citations would include Sherry (1983, 1987a, 1987b).] Moreover, a perusal of the science studies literature would reveal that each of these very same points have been made in connection with what Calder and Tybout would count as empirical science.
ON THE "WHY" QUESTION
Perhaps the most important question that defenders of interpretivism in consumer behavior must answer is: why interpretivism? While many in consumer research have engaged in such studies, with few exceptions (e.g., Sherry 1987b; Hudson and Ozanne 1988), these writers have not been keen to cash out the reasons why interpretive methods evolved as an alternative to the application of the alleged methods of the natural sciences to the study of human behavior. This is puzzling in light of the fact that the so-called Geistes-wissenschaften debate has been going on in social science for more than a hundred years.
The fact of the matter is that there are reasons why some social scientists have found "positivism" (in all of its various incarnations) inappropriate for human studies. While one could (and some authors have) devoted entire volumes to this issue, I will use only a single illustration from consumer research to give but the slightest hint of what some have found objectionable in certain types of experimental consumer behavior.
The study in question was conducted by Tybout, Sternthal and Calder (1983) and provides a quintessential example of what (for lack of a better name) I shall call "psychological instrumentalism." Instrumentalism is the view that the "unobservable" theoretical constructs mentioned in a theory have no "real world" referents. (Ironically, Calder and Tybout's (1987) hero, Karl Popper, is a strident anti-instrumentalist! (Popper 1962)). That is to say, "they .. exist" only at an abstract level" (Sternthal et al. 1987, p. 115). Or as Sternthal (1987) recently put it, they are to be found in the "head of the researcher". This entails that, "Theories are best viewed as heuristics that are useful in explaining a phenomenon" (Sternthal et al. 1987, p. 120). Thus, "Instrumentalism views theories merely as calculating devices that generate useful predictions. . . " (Anderson 1982, p. 20). On this view, theory testing is a comparative process in which the superior theory is the one that explains (predicts) more findings with the same number of constructs as its rivals or requires fewer constructs to explain (predict) those findings.
The best known example of instrumentalism in the social sciences is mainstream neoclassical economics (Anderson 1982, 1986). The extremes of economic instrumentalism in consumer behavior can be found in the work of Becker (1965, 1976, 1981). The problem with instrumentalism is that it places no constraints on the "explanatory" concepts that may be postulated in a theory, and it (allegedly) admits of no other evaluative criteria than "prediction". As long as the theory "out-predicts" its rivals, the ontological status of the theory's concepts cannot be questioned. Indeed, in his seminal work on the topic, Friedman (1953) argues that no other criteria are relevant to a theory's veridicality just so long as it produces "confirmed" predictions. Thus, theorists such as Becker (1976) can assert that households attempt to maximize a "utility function" subject to the constraints of a "production function" and "full income" by solving a "Lagrangian equation". If these axioms produce accurate "predictions", the theory can be judged superior to competitor theories, because said competitors must invoke the "unnecessary "concept of .. tastes" to explain the same phenomena. (It should be noted that "realism", often viewed as instrumentalism's polar opposite, is equally bankrupt (Laudan 1981, 1984a; Hardin and Rosenberg 1982; van Fraassen 1980; Fine 1986). As such, a position of "ontological agnosticism" is strongly recommended.)
While at an abstract level, the parallels between the instrumentalism of Sternthal et al. and Becker are striking, it may be objected that psychological instrumentalism does not engage in the kind of ontological excesses that one finds in economic theories of consumer behavior. However, on closer examination we may find that, as Wittgenstein (1953) would put it, we are "tricked" by the residuum Of OUT own socialization. That is, we are all raised in a culture in which attitudes, values, beliefs, comprehension, memory, etc., are regularly attributed to ourselves and to others and are frequently invoked as causal determinants of behavior. These terms constitute the ontology of what has been called "folk psychology" (Stich 1983), and it should be clear that contemporary cognitive psychology has been built on the foundation of this ontology. Thus, when we are told by an instrumentalist that a household buys a product because its members "believe" that it will satisfy their needs, we are less likely to recognize the instrumental usage of this term because it is rooted in our everyday discourse. In fact, psychological instrumentalists trade on this tendency in order to give their theories a certain "plausibility". Indeed, in addition to the explicit criterion of "prediction", psychological instrumentalists often use the "shadow" criterion of intuitive plausibility to gain acceptance for their theories. Unfortunately, this plausibility can quickly evaporate under closer scrutiny.
An example may be found in the work of Tybout, Stermhal and Calder (1983) on multiple request effectiveness. While a full critique of this study is beyond the scope of the present paper, the essential points can be made with reference to their experiment III (pp. 286-87). The major objective of the article is to demonstrate that their "version" or "extension" of Tversky and Kahneman's (1973) availability theory is Superior to the extant selfperception and bargaining-concession explanations (Tybout et al. 1983, p. 282).
It is important to note that the original availability hypothesis" stated that, "A person is said to employ the availability heuristic whenever he estimates frequency or probability by the ease with which instances or associations could be brought to mind" (Tversky and Kahneman 1982, p. 164, emphasis added). However, Tybout et al. assert that, "Our version of the availability notion states that individual's decisions depend on the favorableness of the issue-relevant information available in memory" (1983, p. 282, emphasis added). Thus, Tybout et al. not only use a very different "availability" theory, but their approach seems to be a more rigorous conceptualization of availability. Tversky and Kahneman assert that judgements depend only on the ease with which instances can be generated, and they suggest that this may occur "without explicitly retrieving or constructing any instances at all" (1982, p. 166). As they note, Hart (1967) has shown that subjects can accurately assess their ability to remember items even when they cannot recall those items. However, Tybout et al. apparently require information to actually be accessed from memory, and they also require people to make judgements on the valence of this information. Moreover, all ten of Tversky and Kahneman's empirical studies supporting the availability heuristic required subjects to consciously access their "memories" (1973). The issue of "conscious access" becomes important because Hastie and Park (1986) [working firmly within the positivist paradigm] have recently argued that most judgment situations may actually be characterized by what Schatzki (1983) would call unreflective action" (p. 132).
Based on their own empirical work and a review of more than 50 published studies on the memory-judgment relationship, Hastie and Park have proposed a distinction between "on-line" and "memory -based" judgment tasks. In their view, the Tversky/Kahneman availability model is the paradigmatic case of memory-based judgments. Here the subject's decision is assumed to result from the functioning of a mental "judgment operator" with input to the operator coming from long-term memory rather than directly from the external environment. However, they argue that the far more common judgment situation (both in laboratory and natural settings) may be characterized by their on-line model. Here "information for the operator follows a path from the stimulus environment external to the subject into working memory and directly to the judgment operator" (1986, p. 261). They argue further that "true memory-based judgments [i.e., judgments based on recall of issue-relevant information] may be Tare because so many judgments are made on-line (spontaneously) and because when a new judgment must be made in the absence of perceptually available evidence, subjects rely on previous judgments rather than remembered evidence" (1986, p. 263), emphasis added).
Of course, it may be argued here that a subject's use of previous judgments is a memory-based process because on-line decisions require the individual to access judgment conclusions "stored in working memory" (Hastie and Park 1986, p. 260). However, if this is "in fact" the process model being employed it is clearly at odds with Tybout et al.'s (1983) "availability hypothesis" in which "critical request compliance is a judgment that depends on the favorableness of available information" in memory (p. 289, emphasis added).
The significance of the distinction between the on-line and memory-based models for memory-judgment correlations is that, in memory-based decision settings, a direct relationship among evidence, memorability and judgment is predicted on the basis of the availability hypothesis. However, if the judgment is made on-line, Hastie and Park (1986) suggest that any one of four process models may be instantiated: 1.) the two-memory independence hypothesis, 2.) retrieval bias, 3.) encoding bias, and 4.) incongruity -biased encoding. [For case of exposition, I have purposely remained within the cognitive "paradigm" here. However, a case will also be developed for a Wittgensteinian explanation as well (Wittgenstein 1953).] The problem is, depending upon which process model is assumed to be operating, the prediction for the memory-judgment relationship "can be either direct, indirect or null" (Hastie and Park 1986, p. 262). Thus, even if judgments are "actually" made on-line, the data from an experiment may well support a memory-based availability hypothesis. As Lynch and Srull (1982) have noted:
For any set of data, it is possible to draw different inferences about the nature of the mental representation by changing one's assumptions about the processes operating on the stored knowledge base to produce the observed responses... Anderson (1978) maintained that the indeterminancy is so great that one can never draw inferences about memory representations from behavioral (i.e., nonphysiological) data, because any hypothesized representation can be reconciled with an observed response by making appropriate assumptions about the processes that operated... to produce the observed behavior. A less radical view... that we would endorse is that to draw inferences about memory structure from behavioral data, one must simultaneously consider both the memory representation and the processes that act upon it (p. 24, emphasis in original).
The implications of all this for the Tybout et al. (1983) "availability" studies should be clear. Not only have they altered the original theory so that it is no longer clear what version of the Tversky/Kahneman model they are testing; it is similarly unclear if the subjects in their various experiments are making on-line or memory-based judgments. Perhaps this is easiest to see in experiment III. Here subjects in two of the conditions were asked to participate in a 5 minute phone survey (the small request), and were then asked if they would participate in a 15 minute phone survey (the large request). [Subjects in the first condition did not perform the small request, whereas compliant subjects in the second condition did perform the small request.] The results of the study supported the Tybout et al. version of availability theory. However, given the nature of the research setting (phone requests to participate in surveys) it is not obvious that subjects had any information in "memory" on which to base the second judgement. As Hastie and Park (1986) suggest, they may have been relying solely on their prior judgements "stored" in working memory. Thus, the Tybout et al. design raises the question of whether they were, in fact, testing an "availability" (memory-based) hypothesis. In other words, the lack of any process data concerning the correlation between "memory" and "judgment" makes it impossible to even begin to cull the list of competing models.
It must be quickly noted that I am in total agreement with Sternthal, Tybout and Calder's (1987) view that the use of manipulation checks, process measures, and repeated operationalizations is a contingent decision that depends upon the circumstances of each particular study. However, in light of their desire to rule out alternative hypotheses, it seems that their "availability" studies have come up short. Moreover, it is not clear whether the problem stems primarily from their failure to employ a particular set of methods, or from a failure to carefully specify the nature of the process and ontology entailed by their version of availability theory.
Indeed, this approach to theory testing tends to be characteristic of the instrumentalist world view. That is, instrumentalism often encourages a "handsoff" attitude towards research. As long as the theory predicts accurately, one need not be bothered greatly be the "details" of process. As we have seen, however, this lack of attention to process can raise serious questions about the validity of a study. Moreover, ins tru mentalism also plays fast and loose with a theory's ontology. The reluctance of Tybout et al. to clearly specify the meaning of their version of "availability" leaves them open to the sort of criticism emanating from the work of Hastie and Park (1986).
The bottom line here is that it is Sternthal, Tybout and Calder's (1987) version of psychological instrumentalism that may lead consumer research to the dire consequences that Calder and Tybout (1987) attribute to critical relativism. Ironically, the foregoing criticism of their availability research follows directly from critical relativism's chief demand:
To know a theory's mode of production, the criteria by which it is judged, the ideological and value commitments that inform its construction, . . the metaphysical beliefs that underwrite its research program, [and] most importantly. . . . [its] realizable cognitive and practical aims (Anderson 1986, p. 156).
This is why I have argued that critical relativists are actually more "hard-headed" in their evaluation of theory than their positivistic counterparts (Anderson 1986, p. 167). Indeed, it is through this example that we may find a hint of the methodological implications that will follow from critical relativism.
The relativist is not afraid to roll up his or her sleeves in order to dig into a study, theory, Or research program in order to reveal the soft underbelly that may lie within. Moreover, the relativist realizes that theories have always been evaluated on multiple criteria (Laudan 1977, 1984b). To adopt comparative .. predictive" power as the sole arbiter of theoretical disputes is to open the door to the kind of ontological flights of fancy that one observes in neoclassical economics. Finally, psychological instrumentalists will find little support in Laudan's (1977) comparative model of theory evaluation. On Laudan's view, when one is faced with the decision to accept or reject competitive theories that are all flawed along various dimensions, agnosticism is the appropriate position to adopt (1987). Indeed, I would argue that this is exactly the situation in which we find ourselves with respect to the explanation of multiple request effectiveness. We must realize that in science it is no great sin to admit that, at the present time, we lack an adequate explanation for a phenomenon.
Thus, we can see in the Tybout et al. study and in the Sternthal et al. approach to theory testing some of the reasons why their "hyperbolic" form of positivism has been rejected by many researchers in social science. The instrumentalists' lack of concern for the details of process, their excessive emphasis on prediction, and their casual attitude toward the meaning of the key concepts mentioned in their theories has led "positivists" and interpretivists alike to turn away from this approach.
Of course, there are innumerable reasons for the existence of "interpretivism", but space limitations prevent a detailed explication of this enormously complicated issue. Instead, I should like to focus on a particular perspective that undergirds both realist and instrumentalist applications of cognitive psychology in consumer research. As Wittgenstein put it, this is the notion that psychology can treat constructs "in the psychical sphere, as does physics in the physical" (1953, p. 151).
A WITTGENSTEINIAN APPROACH TO "MEMORY"
On the traditional view, psychological predicates (interpreted instrumentally or realistically) can be "operationalized" and can, in turn, be related causally to other mental constructs or behaviors. This so-called "billiard ball" model of social science is one of the main concerns that many interpretivists have with positivism. Under the influence of the later Wittgenstein, many reject this "picture" of the human sciences because it fails at the outset to understand the nature and meaning of mental constructs.
In his later work, Wittgenstein argued that we fail to treat psychological phenomena correctly because we tend to assimilate them all under the rubric of "mental processes". In contrast, Wittgenstein differentiated between two very different types of mental concepts: 1.) states of consciousness (or mental processes) and 2.) dispositions and abilities. The key distinction between them has to do with the "kind" of duration they display. The former have duration that can be continuously monitored and reported upon. Examples would include the sensations of pain or hearing. It is possible (i.e., it makes sense to say) that one's pain is growing more or less and that one has heard a sound for a certain period of time. In contrast, dispositions and abilities display a different type of duration. For one thing, they generally do not cease as the result of a good night's sleep or a redirection of one's attention. Examples include understanding, believing, intending, remembering, etc. Moreover, we typically do not constantly monitor dispositions or abilities. It makes no sense to ask someone: "Since you booked your flights has your intention to go abroad been continuous or has it been interrupted? Obviously, an "interruption" of one's intention would mean that one no longer intended.
Another critical concept in Wittgenstein's later philosophy is the notion of "criteria". A Criterion for ascribing a mental predicate to an individual is not empirical. Rather "a criterion... defines or partially defines that for which it is a criterion" (Hacker 1986, p. 308). On this view, the criterion for ascribing "understanding" to someone is a public demonstration of said understanding. With purposeful "exaggeration for emphasis" (McGinn 1984), Wittgenstein warns us not to think of understanding as a mental construct that an individual holds privately in his or her mind. Instead, it is an ability that can only be shown by some type of action (e.g., speaking French, differentiating an equation, programming a computer etc.). Moreover, the criterion for understanding is the same for the individual as it is for others. Since one can be mistaken about one's ability to understand, say, spoken French, proper public demonstration is necessary even for oneself. This is because part of the meaning of "understanding spoken French" is the ability to do so.
As with "understanding" Wittgenstein argues that it is also potentially misleading to think that "remembering" gets its meaning from a private mental process that takes place in our minds. On this view, remembering is also an ability that requires appropriate public demonstration. What Wittgenstein is trying to do is to get us to recognize that (like "understanding") no one thing counts as remembering and that the referent of "memory" is not a private mental experience.
This can be seen by carrying out a logicogrammatical analysis of the words "memory" and "remember". (Or, as he would put it, we must describe the "language games" played with these words.) This involves a "perspicuous description" of all the ways in which these words are used in ordinary language. (For Wittgenstein, the meaning of a word is given by its actual use.) His objective in all this is to show that, "Remembering has no experiential content" (Wittgenstein 1953, p. 231). Of course, he is not denying that we cannot call up images before the mind's eye". Rather, he is denying that this process" teaches us the correct meaning of the verb to remember". This is something we learn only by socialization in a particular culture.
Consider, for example, the following possible uses of "remember" and "memory": 1.) You are asked for your name by a maitre d' and you give it to him/her straight off. What subjective experience accompanied your remembering your name? 2.) At lunch you are asked what you have been doing for the last three hours and you give the questioner a veridical report. Do detailed "pictures" of your activities "flash before your mind" as you recount your comings and goings during the morning? 3.) Upon request, you give a small electric shock to someone who has never experienced one so he can feel what it is like. Can you do the same thing in the case of memory experience?-so the person can now say: "Yes, now I know what it is like to remember something" (Wittgenstein 1980, p. 24). As Wittgenstein has noted, we can certainly teach the person the use of the words remember and memory, but if he then says:
"Yes, now I have experienced what that is!"... If he were to say so, we should be astonished, and think "What can he have experienced?" For we experience nothing special (1980, p. 24).
What Wittgenstein is trying to do here is to disabuse us of the notion that we come to learn the meaning of remember and memory via private "inner" experiences. However, in the Philosophical Investigations his interlocutor protests that, "You surely cannot deny that, for example, in remembering an inner process takes place" (Wittgenstein 1953, P. 102). To this Wittgenstein replies:
What gives the impression we want to deny anything? When one says "Still, an inner process does take place here"--one wants to go on: "After all, you see it". And it is this inner process that one means by the word "remembering" (1953, p. 102, emphasis in original).
He goes on to state that the belief that he wishes to deny a "fact" of everyday life arises because he is attacking a "truism" of folk psychology - -that remembering is an inner mental process. Instead, what Wittgenstein actually wishes to deny "is that the picture of the inner gives us the correct idea of the use of the word to 'remember... (1953, p. 102).
Of course, neurophysiology shows us that memory" is "inner" in at least one sense. We know, for example, that if the hippocampus and temporal stem on each side of the brain is damaged, the ability to register memories will be lost. However, this is not the kind of inner process that Wittgenstein is concerned to deconstruct. The fact that the ability to remember depends on physiological processes has no bearing on the "misuse" of the term in psychological explanations. Wittgenstein is simply trying to point out that the "psychological" ascription criterion for memory is not an inner "experience" or "feeling" and that we do not learn the use of the word memory via inner ostensive definition.
Implications for Positivism and Interpretivism
The Wittgensteinian perspective on memory is a two-sided coin. On the one hand, it is highly critical of cognitive psychology's conceptualization of the act of remembering and the functioning of memory. On the other hand, it offers a new perspective on these concepts that undergirds a number of interpretivist research programs. Perhaps the most damaging implication for positivistic psychology is Wittgenstein's acausalism. Note that for Wittgenstein the "criterion" for ascribing memory to an individual is proper public demonstration. Recall also that a criterion is not empirical in the sense that it can be cited as "evidence" for some unseen construct called memory. Instead, criteria are definitional. When a person engages in certain actions and activities (within a particular context), it may be said that he Or she "remembered". Remembering is neither a unique phenomenological "experience" nor the actions I undertake when I have "remembered". Perhaps the easiest way to comprehend its criteriological status is to see it as a fusion of both (within the context of a person's Lebens form- -translated as "form of life" and very roughly equivalent to one's culture and "natural history"). Of course, by this point many readers may assume that Wittgenstein is just a behaviorist. However, Wittgenstein explicitly denied this on numerous occasions (see, for example, Wittgenstein 1953, pp. 102-103), and most knowledgeable scholars of ordinary language philosophy agree that his program is radically distinct from behaviorism (especially the behaviorism of B.F. Skinner).
The implications of all this for the treatment of memory in cognitive psychology are straightforward. On a Wittgensteinian construal, there can be no question of invoking memory as a cause of behavior. (Except perhaps in the special sense of Malcolm's (1977) mnemonic causation which instantiates no universal laws.) This is because a person's behavior supplies part of the meaning of the verb "to remember". Their relationship is criteriological (definitional) rather than causal. One's "remembering" cannot be thought of as a mental process temporally prior to behavior, since part of what it means to remember is "remembering behavior". (Note that even if "remembering" were solely an "inner mental process" (whatever that would mean), we would still be unable to say that a person remembered without behavioral criteria!) Hence, there is a codefinitional relationship between the two constructs. As Wittgenstein put it (in a slightly different context), "If this upsets our concepts of causality then it is high time they were upset" (1980, p. 160).
If, on Wittgenstein's view, we cannot treat the relationship between memory and behavior as causal, then a fortiori we are unable to link memory and other "mental constructs" in a causal fashion. Again, this is because we would lack any criterion to assert that something called "memory" was instantiated in the alleged causal train. For example, returning to the Tybout et al. (1983) experiment discussed earlier, differential behavioral effects are attributed to the fact that different types of information are "available" in the memories of the subjects in the different conditions. On this view, participants in the "request own behavior available" treatment would access the contents of their memories and find that "favorable information about their own behavior was no more available than unfavorable information about the request behavior" (Tybout et al. 1983, p. 287). In contrast~ subjects in the "own behavior available" condition would find that "favorable information about their own behavior" was more available (Tybout et al. 1983, p. 287). Given these assumptions, differential behavioral responses were predicted and confirmed.
As noted above, the problem here is that we have no criterion by which to assert that "memory" was even involved in the observed effects. Treatments were applied and differential behaviors were manifested, but there is nothing to show us that "memory" played a role in the outcomes. Indeed, even if we were to conceptualize memory purely as an "inner process"; given the short time that elapsed between the telephone request and the response--it is hard to believe that Tybout et al. envisioned their subjects engaging in a conscious "memory look-up". However, even a casual logico-grammatical analysis of the meaning of the verb "to remember" would reveal that what we call "remembering" is a conscious process. It simply makes no sense to say that I remembered something "unconsciously". (For Wittgenstein "grammar" defined the limits of what it makes sense to say.) Again, the ordinary -language meaning of memory instantiates a conscious process in which a person can display his or her ability to remember.
The Wittgensteinian perspective also raises problems for Hastie and Park's on-line model. Their approach assumes that information from the environment enters "working memory" and proceeds to a "judgement operator" which presumably issues a conclusion that results in some type of verbal or motor behavior. Moreover, "biased retrieval" can occur (when some time has passed since the original judgement) because previous judgements can act to "edit" any "traces" from the original information input stored in "long-term memory". On this view, judgement biases "access" to traces in long-term memory "such that traces that "fit" the judgement are likelier to be found in the memory search Or to be reported at the memory decision stage" (Hastie and Park 1986, p. 260). While Hastie and Park's "Computerese" model of judgement and memory can be found to be in accord with empirical data, we must recall Lynch and Srull's (1982) insightful recognition of the fact that a large number of process models will also be consistent with the body of literature in this field.
Of course, from a Wittgensteinian perspective, talk of "traces", "working memory", "judgement operators", "long-term memory", or "access" makes no sense since we lack criteria for these entities and processes. Moreover, from an ethnomethodological perspective (a branch of "interpretive" sociology that shares much with Wittgensteinian philosophy), such a model makes human beings out to be what Garfinkel, the founder of ethnomethodology, has called "judgemental dopes". In other words, both the Tybout et al. and Hastie and Park models portray human decision making as the inexorable consequence of computational processes that appear to be under minimal human control. In contrast, while both Wittgenstein and Garfinkel place great stress upon the "unreflective" nature of human behavior, both resist the extreme psychologizing found in Tybout et al. and Hastie and Park.
THE ETHNOMETHODOLOGICAL PERSPECTIVE
While space limitations make it impossible to cash out a full-blown ethnomethodological approach to the multiple request phenomenon, it should be clear that ethnomethodology would display the same kind of incommensurability with cognitive psychology that Anderson (1986) demonstrated within positivistic approaches to consumer behavior, and Hudson and Ozanne (1988) illustrated between positivistic and interpretivist perspectives on emotion. While psychological approaches would stress prediction, operationalization of constructs, causal relationships, and an ontology consisting of complex yet unobservable mental processes; ethnomethodology would emphasize an understanding of how social actors maintain a "life-as-usual" stance by making reflective or unreflective choices in social interactions. Here, we can catch a fleeting glimpse of the different axiologies and ontologies of the two approaches. These in turn are reflections of the radically different philosophical world views of the two programs. Indeed, the important point to recognize here is that both perspectives rest on some foundation. While in each case practitioners (due perhaps to training and socialization in their respective programs) may not be fully aware of the philosophical undergirding of their research, the fact remains that there are reasons for alternative approaches to the study of human behavior that go beyond mere whim or personal preference. Moreover, it is on these grounds that the battle for the legitimacy of alternative research programs must be fought.
For example, while I am not a trained edmomethodologist, we can, perhaps, speculate briefly on how ethnomethodology might approach the social process known as "multiple request effectiveness". One of the questions that ethnomethodology is concerned to investigate is: how do social actors sustain the "no thing -unusual - is happening" and "life-as-usual" stance in social interaction? Thus, in a typical "greeting interaction", if the recipient of the initial greeting does not return or acknowledge the greeting, the life-as-usual social setting will have been "breached" (Heritage 1984). In other words, the
initial greeter may accountably infer that "normal circumstances" do not obtain and that "something is up" which needs looking into. Where, for whatever reasons, actors wish to avoid [this outcome], they will engage in the "perceivedly normal"/ normatively provided for conduct (Heritage 1984, pp. 116-117).
We may speculate that one reason that an actor may wish to avoid the "something -is-up" interpretation is that s/he will generally find that his/her interests are served by "appropriate" behavior. Again, as Heritage (1984) has put it:
It is the very reflexivity of the actors, their awareness of the options together with their anticipation of some of the interpretations to which their exercise of the options will give rise, which may ultimately keep them "on the rails" of perceivedly normal/normatively provided for conduct (p. 119, emphasis added).
On Heritage's (1984) view, three conditions must be met for "normal" social interaction to occur in this setting: 1.) social actors know the "greeting" norm, 2.) they are (at least on some occasions) capable of reflexive anticipation of the consequences of breaching the norm, and 3.) they attribute (L) and (2.) to each other.
Garfinkel's ethnomethodology is purposely set in contraposition to the Parsonian notion that everyday social order is maintained by "internalized" norms that emerge from an actor's history of rewards and punishments. On this view, action is "caused" by these internalized rules or norms. While Garfinkel's approach does not deny "normative internalization... as an empirical phenomena" (Heritage 1984, p. 120), it does deny that such rules can determine the specifics of an individual's actions (see, also, Wittgenstein 1953).
More importantly, Garfinkel (1967) wishes to deny the model of the social actor as a rule-governed, psychological "judgmental dope" (p. 67). This means that, on Garfinkel's view, human beings are not automatons constantly under the control of a central nervous system (CNS) that has been either "programmed" or "hardwired" to function in a specific manner in all possible situations. Ethnomethodologists argue that (while much, if not most, of our behavior is "unreflective"), we are nevertheless, free to make choices in social settings (Emerson 1970). Thus, in the greeting example the recipient is free to purposefully ignore the greeting-knowing full well that s/he will be held "normatively accountable" for his or her behavior by the other. However, as noted earlier, social actors "will routinely find that their interests are well served by normatively appropriate conduct" (Heritage 1984, p. 117). Thus, while both Parsons and Garfinkel are interested in explicating the manner in which everyday, routine, institutionalized expectations are carried out, it can be seen that they approach the problem with radically different research programs.
Ethnomethodology and Multiple Requests
Returning to the multiple request phenomenon, we might speculate, for illustrative purposes, on ethnomethodology's approach to this process. For simplicity of exposition, we will continue with Tybout et al.'s (1983) experiment number three. It will be recalled that this is a "foot-in the-door" study in which respondents were contacted by phone and asked to participate in surveys. Based on the results, it is clear that it is something about actually performing the small request that leads subjects in this "treatment" to be more compliant than "subjects" in the other two groups. We have already reviewed Tybout et al.'s "availability hypothesis" explanation for this result. It can now be seen that this is a species of what I have called a "hardwiring" explanation in that a subject's mind is expected to retrieve information from memory and make judgements on its valence. Moreover, this appears to require a conscious "memory look-up" on the part of the individual. However, as noted previously, given the nature of the social interaction in this experiment, it is not clear that subjects had the time to consciously carry out this complex cognitive process. Thus, it appears that Tybout et al.'s proposed process may actually be some version of a "non-conscious" on-line model (Hastie and Park 1986).
If this is the case (as it appears to be for Hastie and Park), then we are working with a model of human beings who are hardwired psychological "judgmental dopes". That is, when faced with a judgement to comply with a large request, the subject's CNS automatically "kicks in" and assesses the relative favorability of information in "memory" and issues a command to produce -one type of verbal response or another.
However, from an ethnomethodologist's perspective, any type of psychological on-line model line model ignores the fact that social interaction is social. Thus, it fails to comprehend that social norms are "doubly constitutive" (Heritage 1984, p. 108). That is, norms serve to maintain the normality of the situation, but they also provide the standard by which breaches are recognized, interpreted, and sanctioned as breaches (Garfinkel 1967). Moreover, while norms are usually "seen but unnoticed... [they are] nevertheless constitutive" in that their observance or their breach will determine the very nature of the actors' perceptions of the social situation (Heritage 1984, p. 110).
Seen But Unnoticed
The "seen but unnoticed" (Garfinkel 1967, p. 36) quality of norms is a crucial aspect of ethnomethodology's Weltanschauung. While the view that norms are constitutive of social settings seems to vitiate their traditional role in sociology as regulative principles, the "constraining" function of such norms is recaptured precisely because ethnomethodology recognizes that actors have a choice in the matter. Thus, most social interaction proceeds smoothly because actors unreflectively follow the "appropriate" norms. However, this is not done because actors have "internalized" the norm in a psychological sense, nor does it result from the functioning of an "atonomous" central nervous system. On ethnomethodology's view, actors always have the choice of breaching the norms and facing the consequences of being normatively accountable to others. While this latter factor probably creates the excruciating normality of everyday life, the cause of this mundane normalcy often goes unnoticed except in the breach.
Waiting for Godot
This can be seen in Garfinkel's (1967) famous breaching experiments. In one study Garfinkel (1963) had an experimenter and a subject play a game of ticktacktoe. The experimenter allowed the subject to go first, whereupon the experimenter erased the S's mark, moved it to another box and made his own mark without giving any hint that what he was doing was out of the ordinary. In 253 trials 75% of the Ss objected to the move or demanded some type of explanation. Many of these Ss were visibly disturbed by the incident. In contrast, subjects who either assumed that a new game was in progress or that the experimenter was playing a practical joke showed little disturbance.
A number of implications follow from this (and other) breaching experiments. First, it shows that mundane social "reality" can fall to pieces when "seen but unnoticed" norms are not followed. As a corollary it may also be observed that the maintenance of social interaction requires what ethnomethodologists often refer to as interpretive "work" in order to sustain social interaction. That is to say, actors must adhere to "perceivedly norm al/norm. ativ el y provided for conduct" (Heritage 1984, p. 119) so that they can get on with their everyday mundane affairs. Second, breaching studies also demonstrate that everyday actors are largely unaware that they are structuring "social reality" through their adherence to "seen but unnoticed" norms. Third, the experiments illustrate the fact that breaches tend to motivate actors to resolve (or normalize) the resultant social anomaly. Finally, it is clear that actors who tried to "normalize" the situation while attempting to maintain the notion that a "standard" game of ticktacktoe was still in process showed the greatest amount of disturbance. In contrast, subjects who gave up ticktacktoe as an interpretive "grid" for understanding the social setting found the experiment far less disturbing.
Other examples can be found in the study of humor, since much of what we find humorous involves non-native breaches. This can be seen, for example, in the dialogue and stage directions that close Act I of Beckett's Waiting for Godot:
Vladimir: We can still part, if you think it would be better.
Estragon: It's not worth while now.
Vladimir: No, it's not worth while now.
Estragon: Well, shall we go? Vladimir: Yes, let's go.
They do not move
Clearly, the humor here derives from the fact that Gogo and Didi agree on a normative Course of action which they leave unfulfilled. Collins (1985) has noted a similar example from a somewhat less literary source:
A few years ago a sketch on television's Monty Python's Flying Circus featured a misleading Hungarian phrasebook. "Can I have a box of matches?" was mistranslated into English along the lines of "I would like to feel your beautiful thighs." The appropriate rebuff in English was mistranslated into Hungarian as "Your eyes are like liquid pools." The phrasebook turned what should have been a routine exchange between a large Hungarian and a meek tobacconist into a violent brawl. The phrasebook introduced disorder into what the participants expected to be a routine orderly interaction (p. 5).
And Now for Something Completely Different
The foregoing should make it clear that social reality" is maintained and sustained by a largely seen but unnoticed" adherence to certain norms and practices; however, the question remains: can ethnomethodology be used as an alternative grid to interpret the multiple request phenomenon? While it is likely that different ethnomethodologists would approach this "problem" in different ways, perhaps some informed speculation can give us a hint of how a radically different (interpretivist) program might deal with this issue.
Let us assume, for the sake of argument, that the following "norm" (NI) is loosely and contingently observed by social actors: "in order to be Perceived as "helpful", try not to disappoint other actors by refusing "reasonable" requests." How might this be played out in the context of multiple request interaction? In the case of the foo t-in-the -door phenomenon, N1 obviously sustains compliance with "reasonable" requests made by strangers. Moreover, having invested some effort that demonstrates to the other that one is helpful, the "subject" would be aware that a refusal to comply with the large request would disappoint the other, and could give-the impression that one is not, in fact, helpful. Indeed, this may be made more salient because the subject has already demonstrated his/her helpfulness in a "publicly observable" fashion.
Turning now to the door-in-the- face interaction, NI implies non-compliance with .. unreasonable" requests made by strangers in that noncompliance does not violate the norm. However, NI does sustain compliance with the small request in that it avoids disappointing the other actor and, at the same time, demonstrates that one is indeed helpful.
It must be quickly added that this is not meant to be a full-blown alternative theory of multiple request effectiveness. (indeed, it is not clear that ethnomethodologists would even wish to "explain" any particular social phenomenon like multiple requests. As Garfinkel (1967) has noted, their interests tend to lie elsewhere.) Thus, the purpose of an ethnomethodological approach to this issue is, at this stage, purely expository. A full fledged theoretical assault on the question would require careful explication, extensive pretesting, and empirical testing.
In this regard, it might be noted, almost parenthetically, that one of the advantages of the "ethnomethodological" approach is that it would be much easier to obtain process data via verbal protocols. Unfortunately, the same can not be said of "non-conscious on-line models" in which the CNS is assumed to function in an autonomous or semiautonomous fashion. Of course, as noted earlier, the ethnomethodological perspective does not assume that individuals consciously follow norms as if they were strict rules of conduct. In this postWittgensteinian age it is no longer possible to assert that human behavior is "rule following behavior" (Wittgenstein 1953). However, the ethnomethodological approach at least holds out the hope that depth inter-views, debriefings, projective techniques, etc. can be used to test the assumed "Process model". Unfortunately, not only are these techniques discouraged by "psychological instrumentalists", but they would be useless if the posited process is that of autonomous CNS functioning.
Of course, it could always be argued that the instantiation of NI amounts to nothing more than ex post theorizing. However, on this basis, it is no different than the postulation of an "availability" explanation. Moreover, the ethnomethodological perspective does not emerge ex nihilo. It is built upon the conceptual foundations laid down by Schutz's .. phenomenological sociology" and Garfinkel's successful attempts at empirically validating the phenomenological program.
Finally, following Anderson (1986) and Hudson and Ozanne (1988), it is important to point out that the "psychological" and ethnomethodological approaches to this phenomenon are largely incommensurable. The axiological, methodological, conceptual, metaphysical, ontological, and ideological/value commitments of the two programs are so different as to render them noncomparable. While it can be seen that both perspectives "cover" or "save" multiple requests, it should also be clear that they do so by completely redefining the subject matter of the problem. Thus, the "interpretive" ethnomethodological approach is no more (and no less) "the application of a given conceptualization, or way of viewing" (Calder and Tybout 1987, p. 138) the problem than is psychological instrumentalism. Moreover, given the empirical and experimental foundation of ethnomethodology (Garfinkel 1967), it cannot be said that the field attempts to "escape from data" or fails to compare interpretations "in order to choose among them" (Calder and Tybout 1987, p. 139).
In the final analysis, however, it 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. On this view, man can always breach the norms of a particular scene with the full knowledge of the interpretive consequences. When we do consumer research, choosing between these two models of "others" is often a matter of training and analytical convenience. But perhaps the question we should be asking is: which model would we like to have applied to Ourselves?
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Paul F. Anderson, Pennsylvania State University
SV - Interpretive Consumer Research | 1989
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Yafeng Fan, Tsinghua University
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