A. Understanding Keynes’s Critique of Econometrics Through his Treatise on Probability

“Keynes’s theory of probability represents a major development within the logical tradition of probability” (^{Lawson, 2009, p. 117}). One of the main differences between the frequentist approach to probability, “the more common notion held within scientific tradition” (^{Lawson, 2009}), and the logical approach to probability held by ^{Keynes (1921)}, is that the frequentist view would consider probability as a “property of the actual physical world, whilst in the logical account [probability] is a property of the way people think about the world” (^{Lawson, 2009, p. 117}). This, however, does not mean that Keynes believed that probability is subjective, because it is not the case that people “are logically free to set their own values for degrees of belief on the basis of human caprice.” In Keynes’s view, probability “is concerned with the degree of belief it is rational to hold in certain conditions” (^{Lawson, 2009, p. 117}) and so probability remains objective. Keynes’s focus is thus not on the empirical but on the rational content of probability. In this case, rationality, according to ^{Carabelli (1988, p. 234)}, should be considered “as practical and contingent, utterly separated from truth and relative to actual limited cognitive conditions.” Hence, probability must necessarily be “grounded on ordinary practice” and has “to be approached by the tools of ordinary language and everyday qualitative and analogical reasoning, rather than by formal and artificial language and by purely quantitative, mathematical tools” (^{Carabelli, 1988, p. 234}).

Keynes’s account of probability “is concerned not so much with truth as with what is rational to believe given the evidence” (^{Lawson, 2009, p. 118}). “In this account all empirical arguments require an initial prob- ability which is usually acquired by analogy” (p. 124), i.e., to the likeness of the objects being compared. The initial probability, however, “may be raised towards certainty by methods of pure induction,” which depend upon the instances and observations made (p. 124). In addition to analogy and induction, Keynes adds a third way of getting to this prior probability when “things are self-evident:” introspection.

According to ^{Keynes (1921, p. 276)}, “before the method of pure induction can be usefully employed to support a substantial argument” an a priori probability must always be found. “The objective of Keynes’s inductive method [...] is to develop generalisations and to analyse ways of increasing their probability both by limiting their universality and by examining the greatest possible diversity of instances” (^{Lawson, 2009, p. 117}).

However, Keynes’s account of probability implies the existence of some restrictive conditions for inference to be possible. Inference would be restricted to an assumption “concerning the character of material laws which, if true, would support the use of inductive methods” (^{Lawson, 2009, p. 154}). Keynes refers to this assumption as atomic uniformity and explains that: “[The] system of the material universe must consist [...] of bodies [...] such that each of them exercises its own separate, independent, and invariable effect [If this were not the case] predictions would be impossible and the inductive method useless” (^{Keynes, 1971, p. 277}).

For most cases, these conditions cannot be met in the context of economics, as “economics is essentially a moral science and not a natural science, [for] it employs introspection and judgments of value” (^{Keynes, 2013, p. 297}, quoted in Lawson & Pesaran, 2009, p. 111).

This means that, for Keynes, “economics too was considered [...] as a ‘logic, a way of thinking.’” The purpose of economics “was seen as that of studying the economic agents’ motives for acting in conditions of uncertainty within the framework of cognitive hypotheses rather than empirical causes” (^{Carabelli, 1988, p. 235}). These hypotheses “were linked to convention and practice,” and “were similar both to those of everyday experience and to artistic fictions [in which] one can find analysis and intuition” (p. 235). To Keynes, therefore, economics was concerned with more than the description of facts and, following his father’s classification, economics “not only mixed descriptions and norms, but was essentially operative; it was indeed merely an ‘art’ [(J. N. Keynes, 1890, p. 35)], that is a ‘system of rules for the attainment of a given end.’” The hypotheses of atomic uniformity could not be met in economics, since “unlike the typical natural science, the material to which [economics] is applied is, in too many respects, not homogenous through time” (^{Keynes, 2013, p. 296}).

B. The Method of Multiple Correlation and its Inapplicability to Non-Homogeneous Economic Phenomena

Following Keynes, homogeneity of phenomena was of paramount importance for inference to make sense.

Thus, this argument was decisive in his critique of econometrics given that economic phenomena were non-homogenous by nature. In relation to Tinbergen’s work, Keynes referred to this matter in a letter to R. Tyler of the League of Nations. Keynes (^{Keynes, 2013, p. 285}) believed that “the logic of applying the method of multiple correlation to unanalysed economic material, which we know to be non-homogenous through time,” that is, a “central question of methodology,” had to be scrutinized first.

If we were dealing with the action of numerically measurable, independent forces, acting with fluctuating relative strength on material constant and homogenous through time, we might be able to use the method of multiple correlation with some confidence [...] In fact we know that [...] these conditions [are] far from being satisfied by the economic material under investigation [...] The coe- fficients arrived at are apparently assumed to be constant for 10 years or for a larger period. Yet, [...] there is no reason at all why they should not be different every year. (^{Keynes, 2013, p. 285})

According to Keynes, inference in economics would not make sense at any rate, given the lack of homogeneity of economic phenomena through time. Keynes’s argument against econometrics draws heavily on the way he characterized economic phenomena, which was different to that of other economists, especially compared to that of econometricians such as Tinbergen. According to Keynes, no inductive claim could be conducted from Tinbergen’s exercise, “not only [because of] the lack of uniformity in the factors of which no specific account is taken [but] also in the case of those which are included in the scheme” (^{Keynes, 1939, p. 567}).

The important point here is that economic variables (omitted or not) should maintain a certain amount of uniformity through time if the econometrician wanted to draw some inferences. Yet, the econometrician faces two fundamental problems here. On the one hand, again, inferential drawing would be impossible in economics because of the nature of economic phenomena. The variables effectively included in the econometric model might not fulfill the condition of uniformity in time, consequently producing a change in the relation with the other variables that could not be considered by an econometrician. On the other hand, researchers relying only on the “passive observation” (^{Haavelmo,1944, p. 16}) of data would not always be able to include all the “potentially important” variables in their model, since some variables, albeit relevant, might not vary during a particular period of time, making it impossible for the passive observer of data to consider them as explanatory.

C. Converging Visions on Testing, Prediction, and Policy Simulation

Since at least the 1950s, one way of testing whether a model is “good” or not has been to assess its predictive accuracy (see ^{Pinzón-Fuchs, 2023}). In the 1930s, however, prediction was far from being considered in this way. Neither Tinbergen nor Keynes thought of prediction as an ultimate criterion to evaluate model performance. Tinbergen, on the one hand, devel- oped a complex “three-stage procedure” to evaluate his models (^{Morgan, 1990, section 4.3}). For Keynes, on the other hand, “there is nothing which [...] suggests that a model that predicts the evidence should receive greater support than a model that is constructed after the evidence is obtained [since] the relation between hypothesis and evidence is purely logical [and so] the issue of which appeared first, the hypothesis or the evidence, [would be] unimportant” (^{Lawson, 2009, p. 122}).

Another way – Keynes’s way – of testing whether a model would be a “good” model was by implementing a special sort of policy simulation. This subsection discusses the visions of econometricians and Keynes about what would account for a sound test of an economic theory, that is, its predictive accuracy or the implementation of an economic policy based on the model the economist is willing to test. Four decades later, ^{Hendry’s (1980)}three golden rules of econometrics, “test, test, and test,” seem to echo Tinbergen’s optimistic belief in econometrics. Prediction and “predictive accuracy,” in ^{Hendry’s (1980)} account, provides a rather severe test for accepting econometric models, if only provisionally, since a pre- diction is presented in the form of a bold claim that is likely to be refuted (^{Lawson & Pesaran, 2009}). While a model that would “merely accommodate” or fit the data, “is often considered to be ad hoc” (^{Lawson & Pesaran, 2009, p. 90}), a model that yields a prediction is actually making a defined, sometimes courageous, and above all bold claim that can potentially be refuted and, hence, a claim that would be considered a Good candidate for testing. Both Tinbergen and Klein’s views of prediction as a means of providing severe tests might be considered forerunners of Hendry’s. For this reason, Klein had a hard time reconciling Keynes and Tinbergen in this aspect.

^{Haavelmo (1943)} also defended the idea of testing economic theory through econometrics but was critical about Tinbergen’s way of presenting his tests. Haavelmo insisted on the importance of “probability theory as the essential missing component which would make the [econometric] approach fruitful” (^{Morgan, 1990, p. 128}). ^{Haavelmo (1943, p. 14)} explained that “[w]hen we speak of testing theories against actual observations we evidently think of only those theories that, perhaps through a long chain of logical operations and additional hypotheses lead to a priori statements about facts.” Thus, “[a] test […] means simply to take the data about which the a priori statement is made, and to see whether the statement is true or false.” Yet, Haavelmo continued:

Suppose the statement turns out to be true. What can we then say about the theory itself? We can say that the facts observed do not give any reason for rejecting the theory. But we might reject the theory on the basis of other facts or on other grounds. Suppose, on the other hand that the statement turns out to be wrong. What we can say then about the theory depends on the characteristics of the theory and the type of a priori statement it makes about the facts [...]

If the statement deduced is assumed to be one of necessity, we would reject the theory when the facts contradict the statement. But if the statement is only supposed to be true ‘almost always’, the possibility of maintaining the theory would still be there [...] If the statement is verified, should we accept the theory as true? Not necessarily, because the same statement might usually be deduced from many different constructions. What we can say is that an eventual rejection of the theory would require further tests against additional facts, or the testing of a different statement deduced from the same theory. Each test that is a success for a theory increases our confidence in that theory for further use. (^{Haavelmo, 1943, pp. 14-15})

For Klein, accuracy of prediction was one important criterion to determine the adequacy of a model (^{Klein & Mariano, 1987}). For example, during the 1970s and 1980s, Klein’s defense of large-scale macroeconometric modeling after Lucas’ critique (^{Lucas, 1976}) was based, among other things, on his claim that macroeconometric models should not be abandoned because they had shown accurate results in forecasting (^{Goutsmedt et al., 2019}). Indeed, in a paper written in 1985, ^{Klein (1985)} directly responded to Lucas’ criticism, fiercely defending macroeconometric models. The first point of his defense consisted in asserting that these models had not failed to anticipate the inflationary surge of the United States economy in the 1970s. Even if Klein recognized a period of ‘significant underestimation’ of the inflation rate by these models – in particular for eight quarterly forecasts between late 1973 and 1975 – he showed that, in the long-term forecasts, the error of the Wharton model was consistently less important when compared to other models.

For ^{Keynes (1971, p. 337)}, however, the “peculiar virtue of prediction [...] is altogether imaginary.” While “the question as to whether a particular hypothesis happens to be propounded before or after their examination is quite irrelevant.” On the contrary, it is “the number of instances examined and the analogy between them [that] are the essential points” to assess the plausibility of a hypothesis. For Keynes, then, accuracy in forecasting is not a testing criterion. In fact, Keynes believed that the way to test a hypothesis is to implement an economic policy based upon it (^{Lawson & Pesaran, 2009, p. 64}), which is quite similar to testing a model based on its capacity to provide a sort of accurate policy simulation.

^{Klein’s (1947)} own observations about the way Keynes arrived at his theories show that policy matters and objectives were the main drivers of the development of his theories. Only after targeting a particular policy problem through economic intuition and a priori knowledge would economic theory appear. A sound economic theory should not necessarily underpin economic policy recommendations. Rather, it is economic policy that should be sound and, through its soundness, it would end up producing coherent economic theories. As sound economic policies would constantly change with the normal flow of societal evolution, so would economic theories also endlessly adapt and change.

Economists can sometimes go very far in the advocacy of proper, sound policy measures on an inadequate formal theory. That such things are possible proves only that practical economics is simply common sense, while theoretical economics is ‘common sense made difficult.’ Keynes had a good idea as to what the troubles were in the economic system in the early years after the 1929 crash – in fact, even before the crash – and he supported policy similar to that built up around the General Theory, but he was not able to formalize his arguments into a satisfactory theoretical mold [...] It was not his theory which led him to practical policies, but practical policies devised to cure honest-to-goodness economic ills which finally led him to his theory. (^{Klein, 1947, p. 31}, emphasis added)

In a nutshell, for ^{Keynes (1921)}, neither probability, statistical inference, nor induction were intended to provide a description or an explanation of the world. They belonged to the branch of speculative knowledge and as such served as guides for life, but they were not subjected to empirical falsification (^{Carabelli, 1988}). Nor were scientific laws, which could not be considered empirical laws. Similarly, Keynes denied the predictive character of theories. Theories were tied to action and thus “had only a projective character, that is, [they] needed hypotheses to operate” (^{Carabelli, 1988, p. 234}).

A. Five Technical Questions Raised by Keynes.

Keynes’s 1939 review contains six major points questioning Tinbergen’s work. The “first five questions concern the specification of econometric equations, [the] sixth, which [Keynes] believed to be in a ‘different department of the argument’ (^{Keynes, 1939, p. 566}), concerns the inductive and predictive value [of the] estimates” (^{Pesaran & Smith, 1985, p. 138}).

(1) Stated in modern terms, the first question raised by Keynes was about the problem of “omitted variables” in the equations. According to Keynes, the econometric method was not a tool for discovering the variables that were missing in the model. Econometrics was constrained by the theory economists provided and, even if the variables proposed by the theoretician were veræ causæ explaining the phenomenon, this did not mean that econometrics could provide any help in completing the theory. The completion of the economic theory was only possible at the level of the construction of hypotheses, which had more to do with intuition than analytical reason, since it was driven by the necessity of producing a clear action under particular circumstances (^{Carabelli, 1988}).

Keynes specifically asked whether:

[He] was right in thinking that the method of multiple correlation analysis essentially depends on the economists having furnished, not merely a list of the significant causes, which is correct so far as it goes, but a complete list? For example suppose three factors are taken into account, it is not enough that these should be in fact veræ causæ; there must be no other significant factor [causing the phenomenon]. If there is a further factor, not taken into account of, then the method is not able to discover the relative quantitative importance of the first three. If so, this means that the method is one neither of discovery nor of criticism. (^{Keynes, 1939, p. 560}, emphasis in the original)

The direct implication of this claim is that econometrics should be regarded only as a measurement tool (^{Boumans, 2010}). In this view, it was not possible to conceive econometrics as a tool for testing theories or for discovering new things about the world that would not be already contained in the theory.

For Tinbergen, as for Keynes, it was clear that it was the economist who had to play the “heuristic role” in economics and not the econometrician. It was the economist’s responsibility to hand over the economic theories containing the complete list of explanatory variables or, in Keynes’s words, “factors, or veræ causæ,” since statistical theory was, on the one hand, restricted to economic theory and, on the other, not able to prove economic theory to be correct.

The part which the statistician can play in this process of analysis must not be misunderstood. The theories which he submits to examination are handed over to him by the economist, and with the economist the responsibility of them must remain; for no statistical test can prove a theory to be correct. (^{Tinbergen 1939, p. 12})

However, statistical theory could “prove [...] theory to be incorrect, or at least incomplete, by showing that it does not cover a particular set of facts” (^{Tinbergen,1939, p. 12}.) and, hence, “statistical theory” or econometrics would contribute to recognizing that not all the relevant variables explaining the phenomenon had been included in the model. That is, that the model had problems of omitted variables. Yet, Tinbergen recognized that “even if the theory appears to be in accordance with the facts, it is still possible that there is another theory, also in accordance with the facts, which is the ‘true’ one” (^{Tinbergen, 1939, p. 12}).

It is worth noting that Tinbergen believed there was a ‘true’ theory underlying the phenomena that ought to be discovered, and that there were two ways of discovering it: (a) by the advent of new facts, and (b) by the advancement of further theoretical investigations. Tinbergen’s practice, however, was not as schizophrenic as his declaration suggests. His own way of conducting research and building models led him to be both a good statistician capable of rigorous data analysis, as well as a well-informed economist who handed over theories grounded both on a priori thinking and empirical evidence. “Tinbergen’s approach to economics has always been a practical one [...] [enabling] him to make important contributions to conceptual and theoretical issues [...] always in the context of a relevant economic problem (^{Tinbergen et al., 1987, p. 117}).

(2) The second point questioned by Keynes was Tinbergen’s assumption that all the variables he included in the model were measurable, and that he could find a way of “supplementing” the model with information about the unmeasurable variables:

The enquiry is, by nature, restricted to the examination of measurable phenomena. Non-measurable phenomena may, of course, at times exercise an important influence on the course of events; and the results of the present analysis must be supplemented by such information about the extent of that influence as can be obtained from other sources. (^{Tinbergen, 1939, p. 11})

Keynes was skeptical about Tinbergen’s way of providing information on these non-measurable factors and claimed that Tinbergen would “withdraw from the operation of the method all those economic problems where political, social and psychological factors, including such things as government policy, the progress of invention and the state of expectation, may be significant” (^{Keynes, 1939, p. 384}).

(3) The third question Keynes asked had to do with the independence of the economic “factors” or variables. This point has already been evoked in the second section of the paper, and I will only mention it briefly. According to Keynes, this point was important “[for], if we are using factors which are not wholly independent, we lay ourselves open to the extraordinarily difficult and deceptive complications of ‘spurious’ correlation” (^{Keynes, 1939, p. 561}).

(4) The fourth point raised by Keynes was about the functional form of the model, that is, about the specification problem, and in particular about the assumption of linearity, which might rule out cyclical factors. Tinbergen had announced that “curvilinear relations [were] considered in [his] studies only in so far as strong evidence exists” (^{Tinbergen, 1939, p. 11}) that the relations between variables present other non-linear forms. In the end, however, Tinbergen treated all the relations between variables as if they were linear relations, since for him linear relations were, overall, good enough approximations of curvilinear relations.

^{Marschak and Lange (1940)} recognized how careful the econometrician should be in “choosing the type of regression function to be fitted” due to “the hidden economic implications of the linearity of Tinbergen’s equations” (^{Marschak & Lange, 1940}, quoted in ^{Hendry & Morgan, 1995, p. 396}). Yet they defended Tinbergen in this respect and claimed that:

Professor Tinbergen’s data [...] do seem to warrant the use of linear functions as a first approximation. Keeping in mind that the linear relationship is a first approximation of any analytic function and taking into account that because of errors of sampling the significant part of a regression curve is restricted to a small section in the neighborhood of the centre of gravity in the scattered diagram, the use of linear functions as approximations appears quite justified. (^{Marschak & Lange, 1940 [1995], p. 396})

(5) The fifth problem brought up by Keynes consisted of the issue of dynamic specification, time-lags, and trends. Indeed, to Keynes, Tinbergen’s only criterion for time-lag determination consisted of a rather arbitrary and sketchy strategy, instead of a well-defined method:

To the best of my understanding, Prof. Tinbergen is not presented with his timelags, as he is with his qualitative analysis, by his economist friends, but invents them for himself. This he seems to do by some sort of trial-and-error-method. That is to say, he fidgets about until he finds a time-lag which does not fit in too badly with the theory he is testing and with the general presuppositions of his method. No example is given of the process of determining time-lags which appear, when they come, to be ready-made [...] The introduction of a trend factor is even more tricky and even less discussed. This reference is not obtained by reference to secular changes in the scale of the economy as a whole, but is strictly related to the factors under discussion [...] This seems rather arbitrary! (^{Keynes, 1939, p. 565})

The way Tinbergen treated time trends “is particularly unsatisfactory and is based on the implicit assumption that all economic variables are subject to a nine-year cycle” and that is why he “bases his regressions on deviations from nine-year moving average trends” (^{Pesaran & Smith, 1985, p. 140}).

B. Tinbergen’s Position

Tinbergen did not naively think that econometrics would just provide a good way of verifying economic theory. In hindsight, he expressed the matter in the following terms:

I [Tinbergen] think that all of us would agree that you do not prove anything by very favourable values of 𝑅” and of the t-values. You only say that you give some sort of green light to the man who has formulated the varia- bles used in the regression, and so the proof can only, if there is such a thing, be given by economic reasoning [...] It cannot be done by statistical thinking and I think we would all agree that this is so. But it does constitute progress if you can say certain things are not correct. (^{Tinbergen et al., 1987, p. 128}, emphasis added)

Keynes and other economists, contemporary or modern, did (and would) certainly agree with Tinbergen’s claim. Yet, Keynes disagreed with Tinbergen about his idea that “a statistical test could prove theory to be incorrect, ‘by showing that it does not cover a particular set of facts’” (^{Carabelli, 1988, p. 192}, italics in the original). As ^{Morgan (1990)} puts it, “Tinbergen defended the wider inductive claims that [...] econometrics was concerned both with discovery and criticism [and he] believed [...] that if the theory was not confirmed by the results, then the inference was that the theory was wrong or insufficient” (^{Morgan, 1990, p. 125}). In This view, Tinbergen defended the idea that “statistical work might result in the introduction of new variables, or forms of variables, not previously considered as important by theory” (^{Morgan, 1990, p. 125}.), precisely what Keynes thought econometrics was incapable of doing.

Thus, for Tinbergen, “[theory] might also be criticized by statistical evidence, if [...] little or no influence was found in the regression relationship for a variable considered important in the theory” (^{Morgan, 1990, p. 125}). ^{Klein (1950)} seems to hold a rather similar position to Tinbergen in this respect:

Of what use is the statistical treatment of this simple model [^{Klein’s (1950}) famous Model I]? It is agreed that this model is very simplified, very aggregative, but, at the same time, it is more than a mere demonstration of various statistical methodologies. The calculations made for this model serve as a test of certain economic hypotheses. If the data were to refute this model, we should have grounds for questioning the validity of the Marxian theory of effective demand. Since the data do not refute the model, we cannot conclude that this theory stands as proved, but we can have more faith in it, or in any other theory that would produce this model, than would be the case if we made no tests at all. (^{Klein, 1950, p. 64})

The latter quotation reveals quite a bit about Klein’s vision of the role of econometrics in testing economic theories. At a first glance, Klein’s position seems to be quite akin to Tinbergen’s. Data cannot prove theory to be right, but it can prove it to be wrong, and hence Klein might use this criterion to discard theories. This would be the idea behind Klein’s quotation if taken out of context. If, however, one pays closer attention not only to the terms employed by Klein, but also to the passage of the book in which this quotation appears, Klein’s position (as well as Tinbergen’s) might appear more sophisticated and slightly more profound. Klein is talking here about the possibility (and even desirability) of multiple hypotheses. He is asserting that if the data confirms the model, any theory that had produced the model is susceptible of being right. This shows Klein’s (and Tinbergen’s) willingness to promote pluralism.

C. Three Conceptions of Models

The controversy about econometrics is at least partly explained by Keynes’s, Tinbergen’s, and Klein’s different ways of understanding what models are and what they should be used for. Indeed, there are many important aspects of Keynes’s understanding of models. The first has to do with the fact that the theories or hypotheses could be considered correct or incorrect if the economist explicitly accepts the conditions imposed by an econometric modeling method. In Carabelli’s words, “only those theories which were homogenous in character with the technique applied could be shown to be incorrect” (^{Carabelli, 1988, p. 295}). “At best only those theories can be shown to be incorrect, which in the view of the economist who advances them, accept as applicable the various conditions of the method proposed by Tinbergen” (^{Keynes, 2013, p. 307}).

This argument is in line with ^{Haavelmo’s (1944, p. iv)} idea of formulating “economic theories in a statistical way, in order to apply probability theory to test the economic hypotheses, as if they were statistical hypotheses.” In that sense, economists “would be accepting that theories and techniques would be homogenous, and so the latter could judge the former to be correct or incorrect” (^{Haavelmo, 1944, p. iv}). And so,

If we [the economists] want to apply statistical inference to testing the hypotheses of economic theory, it implies such a formulation of economic theories that they represent statistical hypotheses, i.e. statements – perhaps very broad ones – regarding certain probability distributions. The belief that we can make use of statistical inference without this link can only be based upon lack of precision in formulating the problems. (^{Haavelmo, 1944, p. iv}, emphasis in the original)

Another important aspect of Keynes’s understanding of models has to do with the usefulness of an economic model as an instrument of thought. A model was not a representation of reality, but a way to inquire and act on that reality. According to Keynes, it was risky to think that an instrument like an econometric model might be turned into something rigid and general, since, in this case, the model’s usefulness as an instrument would be lost:

In economics […] to convert a model into a quantitative formula is to destroy its usefulness as an instrument of thought. Tinbergen endavours to work out the variable quantities in a particular case, or perhaps in the average of several particular cases, and he then suggests that the quantitative formula so obtained has general validity. Yet, in fact, by filling in figures, which one can be quite sure will not apply next time, so far from increasing the value of his instrument, he has destroyed it. (^{Keynes, 2013, p. 300})

To understand Keynes’s fear about the model losing its usefulness as an instrument, it is helpful to recall Keynes’s view on the way people acquire knowledge under uncertain conditions by leaning on previously institutionalized practices:

[...] lacking information about future outcomes of all current choices, people ‘get by’ by making use of their significant knowledge of existing practices and their general situation; they make use of knowledge obtained through their practical involvement in the society in which they live. (Indeed by so acting on the basis of such knowledge people help to constitute those practices.) This is an integral part of the [...] account of behaviour under uncertainty. (^{Lawson, 1985, p. 924})

When applied to the scientific world, Keynes’s conception of the way humans obtain access to knowledge through institutionalized practices helps to understand his fears about how the inattentive use of models might put some important limits to economics. “Similarly ‘scientific’ knowledge is determined by particular people, whose ways of acting and thinking are dependent upon the society in which they live, and who thus obtain knowledge through participating in that society. Social theory itself then is dependent upon social practice” (^{Lawson, 1985, p. 924}). Given the way economists like Tinbergen were using econometric models as ‘representations of the world’ and not as mere tools of investigation, Keynes worried that this new practice would limit the way economists would gain knowledge about the functioning of economic phenomena. “The pointing out of these limitations can be interpreted as an application to econometrics of A Treatise of Probability’s discussion of the interplay between the specific characteristics of the theoretical tool and those of the material under investigation” (^{Carabelli, 1988, p. 295}). Indeed, referring to mathematical probability and statistics, ^{Keynes (1921)} “stressed the limitative conditions of their application to the logical danger which could be caused by blind application of them” (^{Carabelli, 1988, p. 285}).

This blind application of instruments is consistent with Ian ^{Hacking’s (1992; 2002)} argument about the way scientists might use statistical methods in an unreasoned way, as a style of scientific reasoning, once these practices have been stabilized in a scientific milieu. According to Hacking, practitioners can sometimes adopt a style without really understanding the fundamental ideas behind its methods. “This is at its most obvious in ‘cookbooks’ for statistical reasoning prepared for this or that branch of science, psychology, cladistics taxonomy, high energy physics, and so forth” (^{Hacking, 2002, p. 184}). Indeed, “[w]ith no understanding of principles, and perhaps using only a mindless statistical package for the computer, an investigator is able to use statistics without understanding its language in any meaningful way whatsoever (^{Hacking, 2002, p. 184}).

While not explicitly mentioned by ^{Hacking (2002)}, economics does not escape this limitation either. Keynes, “in his discussion with Tinbergen, [...] stressed the partiality of Tinbergen’s theoretical findings, on the basis that the analytical tool adopted automatically reflected its characteristics upon the material examined” (^{Carabelli, 1988, p. 295-6}). This was an argument that had been already anticipated by Alfred Marshall, Keynes’s professor: “He [the mathematician] takes no technical responsibility for the material, and is often unaware how inadequate the material is to bear the strains of his powerful machinery” (^{Marshall, 1890 [1895], p. 644}).

Some years later, ^{Koopmans (1957, p. 170)} claimed that “tools also have a life of their own,” and that even if they are supposed to have “a servant’s status,” they “may […] become our guides, for better or worse.” He goes on to say that “statistical inference becomes available as the result of a self-imposed limitation of the universe of discourse,” and that we should remember that “the sharpness and power of these remarkable tools of inductive reasoning are brought by willingness to adopt a specification of the universe in a form suitable for mathematical analysis (^{Koopmans, 1957, pp. 197-198}).

In this same vein, Keynes (1936 [1964]) criticized the unreasoned use of mathematics due to its lack of precision. He argued that “the object of our analysis is, not to provide a machine, or method of blind manipulation, which will furnish an infallible answer, but to provide ourselves with an organised and orderly method of thinking out particular problems.” To him “this is the nature of economic thinking” and “[a]ny other way of applying our formal principles of thought […] will lead us into error.” Furthermore,

It is a great fault of symbolic pseudo-mathematical methods of formalising a system of economic analysis [...] that they expressly assume strict independence between the factors involved and lose all their cogency and authority if this hypothesis is disallowed; whereas, in ordinary discourse, where we are not blindly manipulating but know all the time what we are doing and what the words mean, we can keep ‘at the back of our heads’ the necessary reserves and qualifications and the adjustments which we shall have to make later on, in a way in which we cannot keep complicated partial differentials ‘at the back’ of several pages of algebra which assume that they all vanish. Too large a proportion of recent ‘mathematical’ economics are mere concoctions, as imprecise as the initial assumptions they rest on, which allow the author to lose sight of the complexities and interdependencies of the real world in a maze of pretentious and unhelpful symbols. (Keynes, 1936 [1964], pp. 297-298)

For Tinbergen, in contrast, models helped in the search for practical solutions, and he did not overly care about realism, since for him “a model is but a stylized version of the economic system” (^{Morgan, 1990, p. 103}). Tinbergen viewed the economy as a system of causal relations, which could be expressed in a model. He explained that:

We may start from the proposition that every change in economic life has a number of proximate causes. These proximate causes themselves have their own proximate causes which in turn are indirect ‘deeper’ causes with respect to the first mentioned change, and so on. Thus a network of causal relationships can be laid out connecting up all the successive changes occurring in an economic community. Apart from causal relationships there will also exist relationships of definition [...] And, finally, there will be technical or institutional connections. All these relationships together form a system of equations [...] each of [which] can be looked upon as a determining equation for one of the elements, explaining what factors influence that element and how large is the effect of a given change in each factor. (^{Tinbergen, 1937, p. 8}, quoted in ^{Morgan, 1990, p. 103})

Tinbergen thought that mathematics was a powerful tool, but only applicable if the model was simple enough. Yet, simplicity had a cost in terms of losing realism and this enhanced the degree of arbitrariness (which Keynes criticized and Tinbergen had no problem in recognizing). Tinbergen would also call this part of the modeling practice, “the ‘art’ of economic research”:

I [Tinbergen] must stress the necessity for simplification. Mathematical treatment is a powerful tool; it is, however, only applicable if the number of elements [of] the system is not too large [...] the whole community has to be schematised to a ‘model’ before anything fruitful can be done. This process of schematisation is, of course, more or less arbitrary. It could, of course, be done in a way other than has here been attempted. In a sense this is the ‘art’ of economic research. (^{Tinbergen, 1937, p. 8}, quoted in ^{Morgan, 1990, p. 103})

Klein’s conception of models was more ambitious than Tinbergen’s regarding realism. Even if Klein was clear that a model could not fully represent the real relations between the variables explaining the phenomena, he was optimistic about the fact that with painstaking work, with a lot of updating, correcting, estimating, re-estimating, thinking, and rethinking of the model, one would slowly converge to a model which would increasingly resemble reality. Klein very rapidly understood that to be able to account for reality in a model, the statistical methods should remain quite flexible and should not act as strait jackets constraining the economic reasoning behind the modeling activity. Indeed, to ^{Klein (1991, pp. 115-116}) “[i]t is important to grasp the simultaneity of the macroeconomy but not necessarily to tie statistical estimation methods exclusively to this property.” Instead, “It is more important to be able to update, correct or revise estimates on the basis of a steady flow of important new information, and very flexible methods of estimation are needed for this purpose.”

The highly flexible methods can be more powerful in simple form than the more complicated procedures [like the maximum likelihood methods]. In particular, for an economy where detailed information is important, it is preferable to aim for large systems [...] and to handle them by relatively flexible, simple statistical methods instead of paying enormous attention to complicated estimation procedures for smaller manageable systems. (^{Klein, 1991, pp. 115-116})

In a way, the three authors agree on their conception of models as instruments, the construction and use of which reveal the underlying mechanisms of the economy. Keynes, of course, is more careful and less optimistic in his opinion of the usefulness that models might provide if one sticks to them. Yet, one could conclude that ^{Morgan and Morrison’s (1999)} claim that models must be built and used by researchers to learn from them, goes in the same direction as that of Keynes, Tinbergen, and Klein:

We do not learn much from looking at a model – we learn from building the model and manipulating it. Just as one needs to use or observe the use of a hammer in order to really understand its function; similarly, models have to be used before they will give up their secrets. In this sense, they have the quality of a technology – the power of the model only becomes apparent in the context of its use. (^{Morgan & Morrison, 1999, p. 12})

A. Klein’s “Methodological Structuralism”

Klein’s methodological approach brings him closer to Keynes’s vision about modeling. In the spirit of ^{Haavelmo (1944)}, Klein thought that the world, which was composed of structural relations, could be investigated by means of models. His methodology might offer a middle ground between Keynes and Tinbergen, given the heavy institutional component in his approach. In fact, Klein might not stand alone in his position. Klein’s view of how the econometric research should be undertaken was strongly influenced by Haavelmo (^{Klein, 1987 & Mariano; 1991}). ^{Nell and Errouaki (2013)} describe Klein’s Methodological Structuralism as an “ontological turn [...] that ensures that socioeconomic reality, understood through fieldwork [or rather survey data in Klein’s particular case], will be what defines the terms of the model, and not the other way around” (^{Nell & Errouaki, 2013, p. xxiii}). The idea is that models should give an account of “what actually exists,” at the same time exhibiting relationships similar to those found in “reality” in a way that is susceptible of being mathematically manipulated or analyzed:

[Klein] approach[es] the explanation of economic events in terms of a social world made up of institutions, roles, responsibilities, powers and so on [and] considers the socio-economic system to be made up of ‘structured objects’ whose powers exist independently of our knowledge or perception [...] The policeman has the power to arrest us, and the President has the power to call up the National Guard, whether we know it or not. These objects, relationships, powers and duties constitute the basis of the causal relationships that economic science describes. Employers can hire and fire workers and can order them around; firms can move capital from place to place opening and closing plants. (^{Nell & Errouaki, 2013, p. 430}, emphasis added)

“An implication of [...] Klein’s methodological structuralism is that the social domain appears to be open, so it must be described by theories that reflect and acknowledge this openness” (^{Nell & Errouaki, 2013, p. 430}). For instance, Keynesian and Marxian theory are both examples of this reflection and acknowledgement. “‘Openness’ means that some of the key probability distributions could shift unexpectedly, for reasons that cannot be foreseen” (^{p. 430}).

B. Taking a Priori Knowledge Into Account: Another Step Closer to Keynes’s Approach

To improve her model, the researcher has the possibility (or the obligation) of introducing more accurate a priori information into the mathematical model, reflecting, for example, the relation of power between employers and employees in the labor market. A priori information is a type of knowledge about the economy as a whole and “is [therefore] independent of the particular sample being used [and] may consist of economic theory, a knowledge of economic institutions, a knowledge of technology, or empirical results from independent samples” (^{Klein, 1957, p. 2}).

A priori information stemming from “knowledge of technology” means that some improvement could be achieved by developing and refining more sophisticated methods of statistical inference. The improvement of this kind of knowledge is much closer to the line of research of other Cowles Commission researchers, notably Marschak and Koopmans (^{Pinzón- Fuchs, 2014}). Klein did not think that these technical improvements were critical for the advancement of econometrics. Rather, he believed that improving the institutional reality and refining the data would decisively contribute to the improvement of econometric modeling: “The building of institutional reality into a priori formulations of economic reality and the refinement of basic data collection have contributed much more to the improvement of empirical econometric results than have more elaborate methods of statistical inference” (^{Klein, 1960, p. 867}).

Of course, this argument is well in line with Keynes’s thinking: “The more complicated and technical the preliminary statistical investigations become, the more prone inquirers are to mistake the statistical description for an inductive generalization” (^{Keynes, 1921, p. 373}). Thus, for Klein, as well as for Keynes, a priori information or knowledge plays a more important role in understanding the economy and building models than the role that statistical and mathematical methods would play.

C. Validity of Models Restricted to Time and Space

A third point on which all three authors seem to converge is their belief that economic models (or even theories) were restricted to time and space. Keynes “believed that any parameters that might be measured in a particular study at a particular time would not apply to the economy in the future” (^{Moggridge, 1973, pp. 296-9}). ^{Klein (1954, p. 279)}, on the other hand, thought that “a workable model must be dynamic and institutional; it must reflect processes through time, and it must take into account the main institutional factors affecting the working of any particular system.” Indeed, for Klein, “different features must be built into adequate models of […] diverse economies.”

^{Koopmans (1941)} underlined the limited validity of ^{Tinbergen’s (1939}) work, but in its defense. Indeed, even if ^{Tinbergen (1939)} emphasized this point and recognized the limited nature of his study in both time and space, Koopmans insisted that:

The problem to be dealt with [...] may be narrowed down to that of finding a quantitative explanation of cyclical movements occurring in a given country during a given period in which no important, or only readily recognized, changes in economic structure took place. Further, in so far as testing of business-cycle theories appears possible, it means testing the relevance of such theories with respect to country and period considered. (^{Koopmans, 1941, p. 158})

E. Not a “Once-and-for-all Job”

Klein promoted the idea that macroeconometric modeling was not a “once-and-for-all-job” (^{Klein 1950}; ^{Klein & Goldberger, 1955}), but rather a practice consisting of rethinking, re-discussing, re-specification, and re-estimation of the models, and the inclusion of new relevant institutional information and data. Indeed, to ^{Klein (1991, p. 115)}, “Quantitative economics is inelegant, very tedious, very repetitive, and capable of forward movement in small increment [sic].” Even if he “admired the elegant theorems that my associates” at the Cowles Commission “produced, [these] seemed to [him] very strong and not very realistic.” Instead, following the “painstaking tradition of Simon Kuznets,” he felt that “if one paid unusual attention to data –– replicated analyses regularly, looked at more detail for the economy, learned as much as possible about realistic economic reaction, and stayed in touch with the economic situation on a daily basis […] it would be possible to use econometric models for guidance, both in the fields of policy application and in pure understanding of the economy.” In the same vein, and as previously stated, Keynes considered the process of developing economic theories or models a never-ending task. The changes in history and in the economy would oblige the economist to continuously revise his theories and models.