I. INTRODUCTION
That scientists behave as disinterested truth seekers was a common assumption among many classical sociologists of science (after Robert K. Merton) and remains a basic, but often implicit, tenet of many contemporary philosophers. According to this assumption, scientists would put their personal interests aside during the empirical assessment of any hypothesis. For instance, many theories of evidence assume that by accumulating evidence, even the most self-interested scientist will have to admit, sooner or later, that either the hypothesis is confirmed or disconfirmed independently of her own preferences. Yet there is no precise methodological mechanism to account for this decision: it is a matter of trust in the personal integrity of every scientist (e.g., Nagel Reference Nagel1961, pp. 494–95).
However, there are many disciplines, especially among the social sciences, in which the accumulation of evidence has not yielded a broad theoretical consensus. It is often argued that personal biases of various kinds prevent many social scientists from attaining consensus, but the underlying rationale (their personal incapability to overcome such prejudices) is no more convincing than the aforementioned appeal to integrity. Indeed, when the incentives are powerful enough, scientists seem to act in their own interest irrespectively of their field (e.g., Krimsky Reference Krimsky2003). In this paper I will explore through a case study an alternative explanation as to why some economists disagreed more than their peers in the natural sciences, in spite of the evidence accumulated.
The intuition that I will develop is this. In the natural sciences, theoretical concepts are considered as unified semantic entities that can be systematically applied in a diversity of contextsFootnote 1. We cannot manipulate these concepts at will in order to avoid evidence contrary to our interests, and hence exclude these items of contrary evidence from the definition. We may rather expect these categories to filter such partial interests through an iterative procedure of self-correction, as Hasok Chang (Reference Chang2004) recently defended in the case of temperature. Thermologists assumed that, independently of the measurement procedure, they were all measuring different manifestations of the same phenomenon, whose observability excluded optional interpretations. Therefore, they were compelled on methodologically grounds to reconcile their results and make them converge under the same theoretical concept (temperature). Even if they had to rely on various conventions, which were arbitrary to a certain extent, the accumulation of thermometrical evidence compelled thermologists to render all their measuring scales coherent, independently of their personal preferences. Coherence acted thus as a built-in methodological mechanism that screened biases and yielded consensus.
It seems as if such coherence cannot be so easily attained in the social sciences. At least, this has been a traditional dilemma of the most mathematised (and, in that respect, more coherent) of them, neoclassical economic theory. The more definitional constraints we impose on its categories, the more difficult it is to capture data and increase its empirical content. Therefore the accusation of formalism arises against neoclassicism. Yet, if we relax the demand for coherence of economic categories in order to allow for their wider application, disagreement as to their proper use seems both inescapable and difficult to overcome. Natural and social scientists may be equally prone to bias (i.e., selecting evidence in according to their particular interests), but there might be no built-in mechanism in the latter’s categories to prevent it.
In this paper, I will illustrate this situation with a case study of an outstanding economist who also became famous for a methodological defense of the role of evidence in the attainment of a scientific consensus in economics. According to Milton Friedman (Reference Friedman and Friedman1953a), economic theory could be considered a scientific discipline inasmuch as it provided a “language” and “a body of substantive hypothesis” that jointly yielded more accurate predictions, independently of the realism of the assumptions employed to obtain these predictions. Friedman’s methodology was originally intended as an exposition of the principles that guided his own research (Hammond Reference Hammond, David, Hands and Mäki1998) and was subsequently adopted by many others in the profession. Paradoxically, in the years to come Friedman turned out to be a controversial economist, whose predictions did not produce much of the desired consensus among his peers in spite of their purported accuracy.
Instead of claiming that ideological biases can blind us against acknowledging the success of our adversaries’ predictions, as Friedman himself almost came to suspect (Friedman and Friedman Reference Friedman and Friedman1998, p. 219), I will argue that Friedman’s methodological prescriptions concerning the definition of the categories of consumption theory relaxed coherence and hindered theoretical consensus. I will discuss first (Section II) how Friedman advocated a definition of the categories of consumption theory on a case-by-case basis in accordance with the interests of the analyst. His underlying motivation was to allow for as many data classifications as possible since this was required to apply Friedman’s statistical technique of choice (linear regression) and obtain predictions (without which the scientific status of economics would seem questionable). There was thus a clear trade-off between predictions and coherence: any attempt to encompass all the possible applications of a single category under a well-articulated definition (as in general equilibrium theory) prevented the accurate description of each particular market analyzed and the acquisition of significant predictions about themFootnote 2.
Yet Friedman’s definitions became easily contestable by anyone who disagreed with either the assumptions or the consequences of the analysis, no matter how accurate the predictions. It was always possible to argue that a different classification of the data was equally cogent. In other words, consumption categories interpreted à la Friedman were not coherent enough to filter personal biases and yield scientific consensus. I will analyze a couple of studies that Friedman considered methodologically exemplary in order to see how the objections concerning the inability of his results to generate consensus were articulated. First (Section III), we will discuss some chapters from his first book, Income from Independent Professional Practice, coauthored with Simon Kuznets, and then (Section IV) the central hypothesis of A Theory of the Consumption Function. Friedman’s approach will appear here as a less inspiring methodological alternative than it is sometimes deemed to be. To conclude, I will discuss to what extent we can attribute the lack of scientific consensus (and therefore theoretical progress) to a lack of definitional coherence.
II. CLASSIFICATIONS AND PREDICTION
The meaning of scientific terms, as used by a given community, is determined either by sense data or by the shared interests of its members. Whereas in the first approach the meaning of a term is fixed (in various degrees) by its reference, in the second one it is rather agreed (more or less explicitly) among its users. In both cases, it is assumed that such determination is robust enough as to secure a certain coherence through all the applications of each term. In this respect, no individual can change at will the meaning of a term in accordance with her particular interests, unless these correspond to either the very nature of its reference or the interests of the rest of the community. Both alternatives have been widely explored by philosophers and sociologists alike.
Less attention has been paid to those scientific terms in which the data do not allow for a uniform categorization, or the interests of the community do not converge in a single definition. This apparently was the case in demand studies when Friedman produced his methodological manifesto. There were conflicting interpretations of demand theory, hinging on the general vs. partial equilibrium divide, the former being less prone than the latter to yield empirical predictions. Friedman’s methodology for positive economics dictated that we should choose among these interpretations in accordance with the accuracy of the predictions they yielded.
In postwar America, a generation of economists educated in the aftermath of the Great Depression were eager to contribute to a well-ordered economic governance, and it was quite a widespread opinion that good predictions were the best means to facilitate such improvements (e.g., Despres et al. Reference Despres, Friedman, Hart, Samuelson and Wallace1950). There was an echo of this concern in Friedman’s methodological essay: if the American economic profession could reach an agreement on which theories were better, their fellow citizens would be able to make an informed decision regarding the different economic policies available. They would be able to choose the one whose expected output (as predicted by positive economics) better suited their interests.
However, in order to obtain these predictions, agreement on the proper theoretical categories to be used was crucial. These categories should allow us to classify data and this was crucial to the application of Friedman’s chosen statistical techniques. Regression analysis, as Ronald Fisher taught it, relied explicitly on a classificatory device: the contingency tables invented by Karl Pearson (Porter Reference Porter1986, pp. 311–14). These tables collected observations in their rows and columns and delivered, in the bivariate case, an intuitive test of their fitness to the distribution pattern required by correlation analysis so that further predictions could be derived through a regression. Yet the classification of data in these tables supposed agreement concerning the definition of the featured categories, so that we could place data in the table without any ambiguity.
Friedman’s statistical training was conducted first under the supervision of a disciple of Pearson (the econometrician Henry Schultz) and, most significantly, at Harold Hotelling’s department at Columbia, one of the very few places in the United States where the theoretical developments introduced by Ronald Fisher were taught and applied to economic issues. The statistical methods that Friedman applied throughout his career were in many ways Fisherian and he was a firm believer in the virtues of simple regressions (Teira Reference Teira2007). We may safely assume that the predictions he had in mind when drafting his methodological piece were yielded by these methods. What types of theoretical categories were more suitable for this approach?
In consumption and income studies, the classification of data depended on categories that had been theoretically defined during the neoclassical revolution in the last quarter of the nineteenth century – though various versions coexisted, depending on times and places, during the following fifty years. While he was still an undergraduate, first in Rutgers and later in Chicago, Friedman was exposed to different readings of Leon Walras and Alfred MarshallFootnote 3. According to the interpretation of the former advocated by Henry Schultz, the equations that articulated general equilibrium theory provided a complete picture of the causal interrelations that articulated the economic system as a whole. Through regression analysis, claimed Schultz, all the relevant links between such factors could be empirically traced to test the theory (Teira Reference Teira2006). Friedman took sides with his economic mentor, Arthur Burns, who granted with Marshall that such an exhaustive representation was admissible in principle, but empirical demand analysis required the division of the causal nexus to focus only on the relevant variables in the market under consideration (Hammond Reference Hammond, David, Hands and Mäki1998). Only after a set of partial solutions had been obtained would the Marshallian theorist consider its combination “into a more or less complete solution of the whole riddle.” In Friedman’s own words, Walras would have provided an “idealized picture of the economic system,” but not an “engine for analyzing concrete problems,” as did Marshall (Friedman Reference Friedman and Friedman1953b, p. 57).
Moreover, Friedman argued that the Walrasian stance was sterile for predictive purposes. Defining each theoretical category in a consistent way throughout the entire economic system required a logical rigor that hindered its empirical application. The classification of market data required analytical filing cases à la Marshall:
Demand and supply are to him [Marshall] concepts for organizing materials, labels in an “analytical filing box.” The “commodity” for which a demand curve is drawn is another label, not a word for a physical or technical entity to be defined once and for all independently of the problem at hand
(Friedman Reference Friedman and Friedman1953b, p. 57).The categories of demand theory were thus classificatory devices to organize empirical data, without the constrictions imposed by the, so to speak, causal rigidness of the Walrasian definitions. To put this in our own terms, the reference of these categories could not be theoretically determined, since the causal connections were far too intricate to be of practical use in the classification of data. Without such classification, as we know, there would be no regressions and hence no predictions. Demand theory would thus not reach the status of positive economics. Therefore, a clear methodological rationale existed for the treatment of the categories of demand theory as analytical filing boxes.
To illustrate the divergence between the Marshallian and Walrasian approaches, let us consider the following example extracted from a 1943 joint paper by Friedman and Allen Wallis on the empirical derivation of indifference functions (Wallis and Friedman Reference Wallis, Friedman, Lange, McYntire and Yntema1942). We depart from a given set of statistical data and we want to analyze the quantitative relation of consumer expenditures to price and income, in order to predict the effect of any change in these on consumption. The definition of an indifference function obliges us to classify the data “once and for all,” by using concepts such as goods, taste factors, and opportunity factors. Yet, argued Friedman, the same items may be arranged under any of these three concepts depending on the particular circumstances “of the problem in hand.” This is why “it is so difficult to specify reasonable conditions for deriving indifference curves from observational data” (Wallis and Friedman Reference Wallis, Friedman, Lange, McYntire and Yntema1942, p. 187). And even in those cases when the obstacle was overcome, the Walrasian approach was usually incapable of yielding correct predictions on data other than those used in their empirical specification, since they lacked “elasticity” to incorporate other data. Rather than wrenching the observable data into a pre-existing theoretical scheme, Friedman advocated a reformulation of our theoretical categories to generalize them (Stigler Reference Stigler1994, p. 1200).Footnote 4
Now, we must also notice that Friedman’s interest in predictions was not strictly epistemological. A pure mathematical analysis of the interrelations between the different sections of an economy, such as Walras’s, would be of theoretical interest per se. But if we wanted economics to play a role in the improvement of social welfare, as many economists of Friedman’s generation did, it was not necessary (they argued) to grasp the complete causal structure of those interdependencies in order to decide how to act (Despres et al. Reference Despres, Friedman, Hart, Samuelson and Wallace1950, p. 512). If accurate predictions concerning the consequences of our policies were available, we could attain some rational consensus on which one to choose: “the role of statistics is to resolve disagreement among people. It’s to bring people together” (Friedman quoted in Hammond Reference Hammond and Caldwell1993, p. 225).
We now have all the ingredients in our analysis: a methodology that relaxed coherence in the definition of the categories of demand theory for the sake of predictions and scientific consensus, which were desired for a mixture of epistemological and practical concerns (though we may well conjecture that the most compelling incentive was provided by the latter). Here is the dilemma: Schultz’s Walrasian framework provided, once and for all, the kind of tight theoretical structure needed for making people converge on their predictions, but these latter were difficult to obtain. Friedman’s Marshallian framework required a previous agreement on the part of the economic profession concerning the definition of the categories of demand for each particular problem. But if such definitional agreement was not reached, the Marshallian economists would find themselves in a difficult position: there would always be a rationale to contest the underlying classification as based on a wrong definition of the theoretical categories involved. In the next two sections we will see how these classifications could work unsanctioned, yet at the cost of not yielding the consensus that Friedman strived to attain.
III. INCOME FROM INDEPENDENT PROFESSIONAL PRACTICE
So far as my own work is concerned, I should not want to judge its importance, but I do feel that Income from Independent Professional Practice (written jointly with Simon Kuznets), particularly chapters 3 and 4, embodies the appropriate methodological approach in respect to the combination of empirical and theoretical analysis”
(Friedman to E. B. Wilson, 1946; see Stigler Reference Stigler1994, p. 1200).Income from Independent Professional Practice was the result of Friedman’s first assignment at the NBER, which he joined in 1937 in order to work on income distribution in the United States with Simon Kuznets (Friedman and Friedman Reference Friedman and Friedman1998, p. 68). Having completed a first draft, Kuznets asked Friedman to revise and extend it. The final version was finished about 1941, though it would take four more years to get it published. In 1946, Friedman was awarded his doctoral degree at Columbia. His dissertation consisted of a manuscript derived from the book. Let us focus on the two chapters that Friedman found methodologically most satisfactory and a clear anticipation of his 1953 essay.
Friedman is responsible for the third chapter and the second section of the fourth, where we found the analyses that I will here discuss (Friedman and Kuznets Reference Friedman and Kuznets1954, p. xii). These two chapters consist of 110 pages organized as follows: a thorough statistical discussion of income data drawn from five different professions is carried out in the first 90 pages, while the remaining 20 focus on a demand theoretical analysis of the differences in average income between two of the professions, medicine and dentistry. The first part delivers a sort of analytical description of the data from which a hypothesis is derived: professional workers “constitute a “noncompeting” group” as their number (and hence their income) is not exclusively determined by the “relative attractiveness of professional and nonprofessional work,” but by the number of prospective students who count on the particular resources required to pursue the career in question (Friedman and Kuznets 1945, p. 93). The second part addresses a more specific issue, whether licenses may restrict competitive access to medical practice and therefore account for the observed differences in average income between physicians and dentists. Given that both professions require similar abilities and training, we should expect the prospective practitioners to choose between them mainly on the basis of their respective “level of return” (Friedman and Kuznets 1945, p. 123). The theoretical issue at stake is whether their respective average income corresponds to the equilibrium level:
[I]f entry into the two professions were equally easy or difficult, one might expect an adjustment of the levels of return in them that would equalize their net attractiveness in the eyes of a considerable fraction of those in a position to choose between them
(Friedman and Kuznets 1945, p. 124).The way the issue was addressed exemplifies what I take to be the methodological core of Friedman’s Marshallian approach. In order to render the initial statistical analysis significant in a demand theoretical setting, and so to decide whether the markets for dentists and physicians were in equilibrium, the theory was to be reformulated so as to “generalize the observable data.” This was accomplished in two methodologically crucial steps.
First, Friedman took the arithmetical mean measuring the level of income as a proxy for the utilitarian considerations that theoretically account for the choice of profession by prospective practitioners. The expected mean income would determine individual decisions concerning which career to pursue in order to balance its expected costs (Friedman and Kuznets 1945, pp. 65, 145). Choosing according to this “summary figure” would yield a theoretically significant result: even if the individual is unaware of such a statistical decision rule (Friedman and Kuznets 1945, p. 96), prospective entrants as a whole would decide their career in such a way as to attain a negatively sloped demand curve in accordance with utility theoryFootnote 5. No rationale is provided to justify such a step, though Marshall’s authority may be certainly be invoked at this point (Friedman Reference Friedman1949).
Friedman’s second step consisted in stating a statistical definition of the quantities and prices of the commodities that dentists and physicians sell, since the relevant “unit of service” as well as its cost – so easy to state theoretically – was in fact far from obvious (Friedman and Kuznets 1945, p. 155). As for prices, they could be approximated only by the global amount of money the consumers as a whole are willing to spend for those services (Friedman and Kuznets 1945, p. 158). Since this partially depends on the number of practitioners supplying them, a demand curve for medical services will be traced in which the “price” will correspond to the average net income per doctor and the “quantity” to the number of them operating in a given market once the appropriate ceteris paribus clauses are arranged (ibid.). Correspondingly, the supply curve of entrants will be drawn by taking the practicing professional as the “unit of service” and his expected mean income (ceteris paribus) as its “price” (Friedman and Kuznets 1945, p. 156). However, the data did not allow for a curve to be drawn (p. 161).
Therefore, to deal with theoretical categories as filing cases amounts to equating them with certain available statistical measures that classify the data in a way that is considered relevant “in view of the problem at hand.” No theoretical constraint on the definition of these categories is to be taken into account, even though the resulting concept may seem dubious from a purely analytical standpoint. However, it might be justified on the basis of the practical interest of the results so obtained.
The analysis is necessarily conjectural and our quantitative results are only a rough approximation. But the problem is real, and a rough approximation seems better than none
(Friedman and Friedman Reference Friedman and Friedman1998, p. 8).To see how rough this approximation was (and to what extent it justified Friedman’s methodological strategy), take for instance the discussion of the income equilibrium level for dentists and physicians, which was conducted by Friedman and Kuznets by means of regression analyses performed separately on the 1934 and 1936 data for the following variables: per capita income of both professions, their number per 10,000 population and general per capita income (Friedman and Kuznets 1945, pp. 161–173). The equilibrium difference in income between the two would be the one that made both professions equally attractive to prospective entrants, taking into account the relative demand for their respective services. However, the regressions were not good enough to discern what particular rise in the ratio of physicians to dentists would be needed to reduce the ratios of their incomes to a level close to equilibrium (which was informally estimated to be about a 17 percent difference: Friedman and Kuznets 1945, pp. 132, 172). Given that the observed difference amounted to a 32 percent, the authors could wonder whether it was to be explained as a result of “free and moderately rational choice,” or of an entry barrier in the form of medical licensing instead (Friedman and Kuznets 1945, pp. 125).
Even if such statistical analysis might seem in many ways inconclusive, Friedman and Kuznets suggested that the American Medical Association may be guilty of monopolistic practices. This sparked a controversy within the NBER delaying publication of the book for several years (Friedman and Friedman Reference Friedman and Friedman1998, p. 74). It finally went to print with a “Director’s comment” by Carl Noyes (Friedman and Kuznets 1945, pp. 405–410), who stated certain “reservations” over the scientific validity of the results obtained in chapters 3 and 4. Noyes argued that these results could have been different had the authors introduced additional distinctions (e.g., specialists vs. general practitioners) in their analysis – in other words, if they had used a different classification of the data. Indeed Noyes’ concern was shared by some reviewers who nevertheless praised the statistical effort undertook by Kuznets and Friedman (in the spirit that a prediction is always better than none):
This reviewer tends to agree with a comment made by C. R. Noyes to the effect that the assumptions made about the differences between these two professions were of such an arbitrary nature as to render highly untenable the statement that doctors restrict entry into their profession more than dentists
(Anderson Reference Anderson1946, 400; see also Barna Reference Barna1947).To put all this in our terms, the reference of the categories of demand theory in this market was either too general (the “unit of service” of the commodity) or simply unobservable (utility), and hence could not be discerned directly in the data. Friedman and Kuznets opted for identifying various statistical indexes that provided a data classification intuitively plausible and good enough for predictive purposes. We cannot discern whether any sort of personal bias (for or against the American Medical Association) motivated either the two authors or the NBER director but, if it existed, the predictions so obtained could not filter those biases out. Other classifications according to the interests of the analyst were no less legitimate and, in case of disagreement, demand theory could not dictate which one provided a more coherent interpretation.
However, Income from Independent Professional practice did not set a research agenda whose further development could have provided some sort of test of our conclusion. This will be now found in our second text under analysis, A Theory of the Consumption Function.
IV. A THEORY OF THE CONSUMPTION FUNCTION
A Theory of the Consumption Function, published in 1957, comes closer than anything else that I have written to adhering faithfully to the precepts of my essay on methodology. That is one, but by no means the only, reason why I have long regarded it as my best purely scientific contribution, though not the most influential
(Friedman and Friedman Reference Friedman and Friedman1998, p. 222).In 1951 Friedman wrote a four-page manuscript in which he developed a hypothesis on consumer behavior that would allow for the analysis of aggregate data on consumption (Friedman 1957, p. 13). From this seed would spring, six years later, A Theory of the Consumption Function. In this section, we intend to develop a methodological analysis of the formulation of this theory, with a particular focus on its alleged methodological superiority with respect to Income from Independent Professional practice.
The central element in the hypothesis is a result of Friedman’s studies under Kuznets: the distinction between transitory and permanent aspects in the income data (Friedman and Friedman Reference Friedman and Friedman1998, p. 225). Rather than conferring a statistical interpretation on concepts already available, Friedman would coin new ideas on the basis, again, of pre-existing statistical distinctions.
Let us first introduce the theoretical concepts that Friedman took as his starting point. The consumption function establishes the relationship between aggregate consumption, or aggregate savings, and aggregate income (Friedman 1957, p. 17). Formally, this is a function 
, where the variables stand for the wealth in a given year (W 1) and the interest rate (i), wealth being in turn a function of its income – the expected income in a year – and again the interest rate.
From a theoretical standpoint, it is supposed that the agent’s preference can be represented along the distribution of his consumption by means of indifference curves. To the usual premises (negative slope, convexity) Friedman adds the absence of a temporal preference (Friedman Reference Friedman1957, p. 28) in order to obtain a particular form of the function for permanent consumption cp:
where u stands for the “utility factors” and w for the proportion between nonhuman wealth and permanent income (Friedman Reference Friedman1957, p. 17). The intuition underlying this additional assumption is that individuals do not usually consume according to the short-term fluctuations in their income, but rather adjust it to a certain average, which would be the permanent income. This theoretical concept cannot be directly equated to the current receipts that measured income in most statistical studies (Friedman Reference Friedman1957, p. 10). Moreover, the income earned by a consumption unit during a certain period of time is by definition unobservable. According to Friedman, if we consider permanent income to be the quantity that a consumption unit might expend without its wealth being thereby affected (Friedman Reference Friedman1957, pp. 17, 20–21), we must admit – even though it may seem embarrassingly obvious (Friedman and Friedman Reference Friedman and Friedman1998, p. 225) – that such quantity will depend on the income which the unit expects to earn in a period of time somewhat longer than that regarded by the data. Now this is an expectancy that is not directly reflected in these data.Footnote 6 And the same applies to permanent consumption. Two of the variables that articulate the hypothesis on the relationship between consumption and income are therefore unobservable for any individual consumer unit (Friedman Reference Friedman1957, p. 20).
So far, we may analyze Friedman’s hypothesis as a purely theoretical result, akin to the Hicksian concept of income (among others). But we may also appraise it as a Marshallian reformulation of an existing theory to generalize certain patterns observed in the data. Friedman’s distinction between permanent and transitory components in income was inspired, as he explicitly acknowledged, by a review published by his statistical mentor, Harold Hotelling, in 1933 (Friedman and Kuznets 1945, p. 331n; Friedman Reference Friedman1957, p. 53n; see also Stigler Reference Stigler1996). Hotelling diagnosed a regression fallacy committed by Horace Secrist in The Triumph of Mediocrity in Business: to affirm the existence of a convergent trend between the respective means of several sets of data on annual business profit. These sets had been arranged in accordance with the initial profit of each firm, so that their respective means in successive years will be conditionalized on this value and will tend to the overall mean of the data. In other words, the variance among means of groups will diminish, since the transient component (exceptional good or bad profits) will be cancelled throughout the years coming closer to (regressing toward) the overall mean. Therein lies the fallacy of affirming this purely statistical convergence as an economic fact.
Fisher’s analysis of variance provided a technique to decompose intraclass and interclass correlation, which also provided a significance test for linear regressions. Friedman learned about the technique from Hotelling in Columbia, or directly from Fisher’s Statistical Methods for Research Workers (which Friedman considered “the serious man’s introduction to statistics”). If we had to deal with a series of correlated measurements of a given variable fluctuating stochastically over time, classified into different arrays, the analysis of variance yielded a statistically relevant tool to improve the predictions that we may thereby obtain.
Friedman may have well wondered if there was a theoretical counterpart for this statistical classification in economic theory. Income was certainly one such variable, and it made perfect sense to decompose it into a permanent and transient part to analyze its fluctuations. Yet no assumption was made as to the particular mechanism that would have allowed each particular individual to carry out such decomposition. What mattered most was to read the aggregate data series “as if they had regarded their income and their consumption as the sum of two such components, and as if the relation between the permanent components is the one suggested by our theoretical analysis” (Friedman Reference Friedman1957, p. 41). Conforming to his methodological stance, Friedman viewed the predictions that we could obtain as the only justification needed to grant such assumption, independently of both its realism and of the particular theoretical connections that allowed for the derivation of the hypothesis.
But these predictions, again, depended on the classification of the data that we could obtain on the basis of this decomposition. And, as Friedman occasionally acknowledged, the division of permanent and transitory income “is, of course, in part arbitrary, and just where to draw the line may well depend on the particular application.” Marshallianism was here once more affirmed. Indeed, the central assumption as to the empirical testability of the hypothesis is that the correlation between the transitory components of both income and consumption is null (Friedman Reference Friedman1957, p. 27; Hirsch and De Marchi Reference Hirsch and De Marchi1990, p. 201), which implied that that transitory income does not affect the consumer unit’s planned consumption. But what counts as permanent or transitory? As Chao observes,
Friedman argued that in fact consumers are able to use their windfall receipts on planned consumption, whereas windfall receipts are usually statistically recorded as transitory income. Friedman concluded that unexpected windfall receipts should be regarded as transitory income and expected receipts regarded as permanent income
(Chao Reference Chao2003, p. 87).The problem is that to identify such distinctions in the data in a non-arbitrary way we should be rely on a theoretical model of how individuals form expectations, allowing for some sort of precise empirical control. But this is precisely the sort of theoretical flexibility that “as if” reasoning grants and the Marshallian stance justifies. Friedman’s methodology allows us to identify theoretical categories and statistical indexes without theoretical constrictions, thus transforming the former into filing boxes according to our particular needs. Yet such needs may vary. Hence the predictions themselves will not reconcile our differences if we are led to question our classificatory assumptions.
Indeed some reviewers initially noticed that the intuition captured in the hypothesis was very plausible and the ensuing statistical analysis deserved all praise, but the theoretical underpinnings of Friedman’s model were much more dubious (e.g., Champernowne 1958, Schultze Reference Schultze1958). Nonetheless, it was unanimously considered as worth developing, which subsequently happened in the following decades. We will not follow in detail the debate on the empirical tests the model went through, but will rely instead of the overall assessment provided by Tom Mayer almost twenty years later. As he put it (Mayer Reference Mayer1972, p. 6), the testing of the different theories of the consumption function had not yielded any significant consensus. Most economists disregarded those tests previously published by others “in the quaint belief that one’s own test – being one’s own – obviously deserves more credence.” Mayer tried to survey and ponder all the evidence gathered by both supporters and critics in order to ascertain which theory was better. He concluded that the main implications of Friedman’s hypothesis were not satisfactorily proven, the reason being that
[S]omeone who insists on really rigorous confirmation or disconfirmation must accept the agnostic verdict that for now this hypothesis is neither confirmed nor disconfirmed. But if one is willing to work with the conventional definition of consumption, and to accept the assumption that the yield on transitory income is less than, say 50 percent – hardly a wild assumption – then there is evidence … that the transitory income elasticity of consumption is greater than zero
(Mayer Reference Mayer1972, p. 348).“The conventional definition of consumption” was based on the purchase of consumer goods as reported in the national income accounts, whereas others who advocated a theoretically grounded definition referred only to the actual destruction of consumer goods by use, not to the reported purchase of consumer goods (Mayer Reference Mayer1972, pp. 12–15). The problem was that no relevant data were then available to test this, and it might be argued that the durable goods included the consumer expenditures accounted for the positive correlation with transitory income. Herein lies the importance of Mayer’s initial caveat.
We are again caught in a methodological trap: the accumulation of empirically testable predictions will not produce a consensus if there is no previous agreement on the classification of data. But if we opted for more rigorous definitions to attain such classificatory agreement we might be unable to classify the data from which the predictions could be derived. In the empirical analysis of Friedman’s hypothesis it was customary to use both definitions of consumption, one in the formal exposition of the theories and the other in much of the testing of them. Therefore, it was always optional for the reader, according to her particular interests, to appraise the tests as if they were probing “a series of propositions which differ from these theories [e.g., permanent income theory (DTS)] in their definition of consumption.”
V. CONCLUDING REMARKS
Friedman’s methodology did not guarantee coherence in the definition and application of the categories of demand theory, but rather praised their disunity. I contend that this is why it failed to yield a wide professional consensus. My conjecture is that all sorts of interests might have prevented this: a long as there was an incentive to disagree, Friedman’s methodological stance delivered a Marshallian argument to justify it. Loose definitions are acceptable as long as they allow us to grasp the specificity of market data and obtain predictions therefrom.
The debate on Friedman’s methodological essay has focused mostly on matters of epistemic principle: namely, whether his case against the realism of assumptions was philosophically sound, either as it stood or combined with other philosophical ideas (e.g., falsationism, pragmatism, etc.). Friedman’s methodological ambiguity is proverbial, and his self-proclaimed Marshallianism is no exception in this respect. As Hirsch and De Marchi (Reference Hirsch and De Marchi1990, p. 37) warn, we may not be able to derive a consistent interpretation of the Marshallian–Walrasian distinction if we take it as it appears in Friedman’s works. Yet if we connect it to the statistical techniques he used to obtain predictions, the idea of treating theoretical categories as filing cases seems unambiguous: depending on whether our definition of these was particular or general, we would be able to obtain different classifications of the data.
Why economists should agree on a particular classification was one of the many questions that Friedman left unaddressed. He may have thought that most economists were as disinterested as he was (Friedman and Friedman Reference Friedman and Friedman1998, pp. 218–19), but he was providing methodological arguments for precisely those who were not so they could justify their disagreement. In this respect, Friedman was wrong if he thought that the methodology he was advocating was similar to that of physics (1953a. pp. 16–19). If we take Chang’s analysis (2004) as counterexample, we see that the coherence of the theoretical categories in use is crucial to the progress of empirical measurement even when we do not have direct access to the world. Whether the Walrasian approach could do it better is a methodological question that we should leave open here.
