13. Tacit Preachments are the Worst Kind

CHAPTER 13

Tacit Preachments are the Worst Kind*

PREACHING AND COUNTERMETHODOLOGY

Some years ago I gave a talk on “The Curse of Methodology.” That unfortunate title appeared to deny that methodology comes in good varieties as well as bad. Still, good methodology is mostly countermethodology, which strives to free working economists from methodological pressures. The worst preachments, which were and remain my main target, are the pervasive, tacit, dimly identified kind. Countermethodology can drag them into the open, exposing them to inspection and, when appropriate, to ridicule. As if to ward off this exposure, however, the practitioners of tacit methodology appear to taboo explicit method-talk.¹

I offer this and other remarks about the state of academic economics not as confident assertions but as conjectures and as possible explanations of what we do observe. We have an opportunity to confess our suspicions and to compare and check them out. I quote and paraphrase scholars whose writings document my points or who share my perceptions and I also use footnotes all more extensively than precepts of good writing style might otherwise recommend. Invoking respectable company itself proves nothing, but it assuages my uneasiness.

In part, admittedly, I’ll be expressing personal pique. Even some experiences with explicit methodologizing prod me. They include all too many “Austrian” seminars at two or three universities in which discussion routinely degenerated from the substantive to the methodological. I have seen dissertation-writers (at the University of Virginia) badgered about what their models might be or what hypotheses they were testing (and have experienced some badgering myself). I have heard all too much praise of methodological articles that did not rise above pointless profundity.²

Some economists, then, though a minority, are fascinated with methodology. Why? Could they be delighted with their own breadth of learning, as in epistemology and the philosophy of science? Could they believe that such profundity and wisdom must have great significance, somehow, for their own field? Perhaps it helps make a splash to propose importing into economics, even without reference to any genuine questions or problems, ideas and techniques lifted from other fields. Examples include notions of Newtonian and Bergsonian time, concepts of hermeneutics, psychological notions, and mathematical techniques from engineering.

Far be it from me to taboo such borrowings, but the test should be not whether they confer a supposed cachet on the borrowers but whether they further genuine investigations. Nor do I want to lecture methodologists against the pleasure of wallowing in their favorite profundities—not unless they expect other people admiringly to join in.

Methodologists get a handle on other people as teachers, dissertation supervisors, journal editors and referees, conference organizers, participants in tenure and promotion decisions, writers of letters of recommendation, and members of fellowship and research committees. People in such roles almost necessarily issue advice or apply requirements. Those people may deserve some advice in turn, even though it may sound like methodology itself.

Donald McCloskey (1985, esp. pp. 24-26) distinguishes three levels of methodology. The bottom level, unobjectionable and necessary, consists of teaching nuts and bolts like how to construct an Edgeworth box, run a regression, and punctuate a sentence. The top level, “Sprachethik,” also unobjectionable, calls for constructive dialogue. Scholars should try to communicate clearly and avoid shouting and other tricks of intimidation.

On the middle level we find pronouncements about mathematics, econometrics, modeling, empiricism, armchair theorizing, methodological individualism, use of aggregates and averages, use of questionnaires, experimentation, and so on. Methodologists discuss whether the supposed methods of the natural sciences belong in economics, whether economics is more like physics or biology, whether notions from anthropology and literary criticism and other disciplines should be imported, and what should be regarded as the Lakatosian hard core of economics. Such middle-level methodologizing is presumptuous and officious.³

Anyone who has refereed for journals knows that hitching onto fads, routine originality, unnecessary polemics, pretentiousness, tedium, and bad writing abound. Methodology will hardly remedy these defects because, for one thing, no single best method is available. The academic division of labor leaves no presumption that all researchers should tackle the same problems in the same way⁴.

Whether the natural and social sciences are fundamentally similar or fundamentally different is a pointless concern. What does “fundamental” mean? All sciences seek propositions of generality and depth (Bauer 1959), seek uniformity amidst superficial diversity, and try to explain initially puzzling phenomena as examples of familiar or potentially familiar generalizations, so that curiosity rests (evoking Machlup’s “aha!”). Success in prediction strengthens the scientist’s hunch that he has found the correct explanation of some phenomenon. All sciences presumably involve what Karl Popper called “conjectures and refutations.” All presumably presuppose similar ideals of scientific integrity and of openness to critical examination. On the other hand, any two sciences differ in their specific subject matters and so in what kinds of empirical observation enter into arousing curiosity, inspiring conjectures, and sifting hypotheses. Human purposiveness and free choice play a role in the social sciences that they cannot play in the natural sciences. Whether this makes the two fields fundamentally different is a mere semantic question.

TACIT METHODOLOGY AT WORK

Here are some signs of poorly articulated methodological thinking:

• Routine questions such as: What hypothesis are you testing? How could it be falsified? What is your model?

• The prestige of falsifiability, with misconceptions about it being reinforced by the slogan against testing a theory by its assumptions to the degree that downright false propositions share in its supposed prestige. (A warning is valid, however, against ostensibly empirical propositions so constructed as to enjoy built-in immunity to any adverse evidence.)

• The prestige of the polar extremes of abstract, high-power theorizing and empirical work, with what counts as “empirical” being practically confined to statistics.

• The associated idea that familiar, dependable facts are by that very token unimportant.

• Knee-jerk insistence on certain styles of argumentation and particularly on “rigor” (about which I’ll have more to say).

• The prestige of working on the frontier.

Examples abound of methodological preconceptions practically foreordaining conclusions or shielding shaky argument or dubious assumptions from scrutiny. They include (in my opinion) the “Austrian” theory of the business cycle, the “pure-time-preference” theory of interest, London-School skepticism of cost-oriented business regulation and indeed of any objective content in the very concept of cost, the rational-expectations school’s insistence on equilibrium modeling, Milton Friedman’s Marshallian demand curve, and widespread mindless recitation of Friedman’s slogan about not testing a theory by its assumptions.

In macroeconomics, the shift of fashion from monetarism to its new-classical version and then on to real business cycles appears to exhibit a methodological basis (as well as some factors discussed later). David Laidler (1990) and Karl Brunner (1989) have diagnosed as much, mentioning an impatience with disequilibrium analysis and a shift of priorities away from empirical evidence toward supposed first principles, microfoundations, and rigor.

EXAMPLES FROM THE NEW CLASSICAL MACROECONOMICS

The new classical macroeconomics, or rational-expectations/equilibrium-always school, provides examples. (Citations and fuller discussion appear in my 1986, pp. 386-393.) The Lucas supply function (Lucas 1973) deals with cyclical fluctuations in aggregate output on the basis of the methodological preconception that sellers are responding to prices only, rather than also to how readily they are finding customers. Notions of pure competition lurk below the surface: the seller can sell all he desires at the going price.

Theorists in this camp seem to believe that monetary expansion, for example, and unexpected monetary expansion in particular, can have an impact on real variables only through price changes—unexpected and misinterpreted changes—and not directly, as by giving sellers more customers. The rival monetary-disequilibrium theory can interpret recovery from depression in a more straightforward way than is available to a theorist unwilling to recognize disequilibrium in the first place.

The idea seems to be afoot in certain circles (or was for a while) that equilibrium modeling is the thing—the technically advanced thing—to be doing in macroeconomics. Robert Lucas and admirers (Lucas 1980, pp. 697,708; Willes 1980, pp. 90, 92) recommended their brand of equilibrium economics for employing technical advances in modeling that simply were unavailable a few years earlier.

Lucas and Sargent (1978, p. 58) appeared to congratulate themselves on the “dramatic development” that the very meaning of the term “equilibrium” had undergone. Sargent (interviewed in Klamer 1983, pp. 67-68) expressed satisfaction with “fancier” notions of equilibrium, “much more complicated” notions of market-clearing, and “fancy new kinds of equilibrium models.” Well, to recommend destabilizing the meaning of words, subverting communication, is the kind of methodologizing that needs to be dragged into the open and inspected.

Suggesting the influence of sheer commitment to a cherished theoretical tradition, Herschel Grossman (1983, p. 240) wrote:

The position that strict application of neoclassical maximization postulates is relevant to macroeconomic developments only in the “long-run” may seem reasonable from an empirical standpoint, but it puts neoclassical economics in a defensive position. It suggests the possibility of a general inability of neoclassical economics to account for short-run economic phenomena.

Yet despite the apparent implication here, disequilibrium is not incompatible with individuals’ efforts to maximize.

The idea seems to be in circulation that an economist who talks about disequilibrium is really talking not about market failure but about his own failure as a model-builder. It is methodologically unfashionable to speak of prices and quantities that are not at their equilibrium values but are only tending toward them at speeds specified only in ad hoc ways. In this connection, Lucas (1980) scorns models containing “free parameters.” Observing and reasoning about disequilibrium processes in a straightforward and therefore relatively nonmathematical manner can be stigmatized as casual and loose, so they escape due attention.

Equilibrium-always theorists presumably know as well as anyone else that atomistic competition is and must be the exception rather than the rule in the real world, that sellers are typically not selling as much of their output or labor as they would like to sell at prevailing prices, that most prices and wages are not determined impersonally but are consciously decided upon (even though decided with an eye on supply and demand), and that these and other circumstances cause or reveal price stickiness. But the theorists do not know these facts officially, not in a methodologically reputable way.

They are inclined to recite the slogan that (in the paraphrase of Willes 1980, p. 91) “theories cannot be judged by the realism of their assumptions,” a slogan reasonable enough in certain contexts and under certain interpretations, yet much abused. Actually, it is necessary to distinguish at least between simplifying assumptions that abstract from unimportant details and assumptions on which the conclusions crucially depend. (Alan Musgrave, 1981, makes enlightening distinctions between negligibility, domain, and heuristic assumptions.)

What assumptions are acceptable simplifications and what ones are crucial to the conclusions depends on the question at hand. “[A]n ecologist concerned about pollution may treat the Black Sea as a closed body of water, the Straits of Marmara being sufficiently narrow for that. But someone considering how to ship goods from London to Odessa should not” (Mayer 1993, p. 38). In investigating the long-run effects on relative prices and quantities of a specified change in wants, resources, technology, or taxes, it is convenient to assume that competition is pure and that markets clear. Things are different in macroeconomics, whose very subject matter is the lapses that do sometimes occur from a high degree of coordination of radically decentralized decisions and activities. When one is investigating how and why separate but interdependent markets fall short of working to perfection, it is fatuous to insist that they are always in equilibrium anyway. More generally, it is fatuous to work with assumptions that rule out the questions to be faced. (It is important, by the way, as Karl Popper taught, to have a question or problem to work on, not a mere topic; Bartley 1990, p. 159.)

Robert Clower and Paul Krugman are among the minority of economists who have spoken out emphatically against the methodology-driven excesses of the equilibrium-always approach. “[T]he approaches of the Keynesians, monetarists, and new classical economists to monetary theory and macroeconomics will get us exactly nowhere,” Clower writes, “because each is founded, one way or another, on the conventional but empirically fallacious assumption that the coordination of economic activities is costless.” While established value theory has indisputable merits, “for some purposes, such as the fruitful analysis of ongoing processes of monetary exchange, models of a very different kind may be required” (1984, “Afterword,” p. 272).

The “Lucas Project,” as Paul Krugman calls it, tried “to build business-cycle theory on maximizing micro foundations... The ramshackle, ad hoc intellectual structures of the 1950s and 1960s were ruthlessly cleared away, making room for the erection of a new structure to be based on secure microfoundations. Unfortunately, that structure never got built” (Krugman 1993, pp. 15-16). The Lucas Project “destroy[ed] the old regime but failed to create a workable new macroeconomics... The true believers in equilibrium business cycles shifted to real-business-cycle theory” (p. 16). “[R]ational-expectations macroeconomics ... collapsed in the face of its own internal contradictions,” leaving macroeconomics in “a terrible state” (p. 18).

In Krugman’s view, “the effort to explain away the apparent real effects of nominal shocks is silly, even if one restricts oneself to domestic evidence. Once one confronts international evidence, however, it becomes an act of almost pathological denial” (1993, p. 17). Krugman mentions tight correlation between nominal and real exchange rates (p. 16). Finding international macroeconomics in a painful dilemma, Krugman alludes to fads and tacit methodologizing: “to write a macroeconomic model with sticky prices is professionally dangerous, but to write one without such rigidities is empirically ridiculous” (p. 17) .⁵

THEMES IN QUASI-TACIT PREACHING: RIGOR

One broad message of Thomas Mayer’s book of 1993 is that academic economics is driven not only by economic reality but also by features of the game itself. Economists attuned to the academic game “frequently act as though the strength of their whole argument is equal to the strength of its strongest link” (1993, p. x). (This strongest-link analogy recurs repeatedly and appropriately, as on pp. 57-63, 80,127-130.1 myself have long used it, for it is an obvious one.) One form of the bias toward excessive formalization “is to lavish tender loving care on those steps of the argument that are rigorous, while paying little attention to the other steps” (p. 66). A related strand of tacit methodology is reductionism—the insistence that all macroeconomics be reduced to microeconomics (pp. 90-97; compare the insistence that psychology be reduced to chemistry and ultimately to physics).

“Rigor” is often taken as self-evidently crucial to respectable economics. At a department meeting years ago, discussion of a proposed course in portfolio management did not concern what of substance the students might learn, or how its subject matter might relate to the body of economic theory or to other courses in the curriculum, or whether it might duplicate existing courses. No, the overriding concern was with whether the prospective instructor would teach the course with due “rigor,” meaning, in the context, teach it as an application of advanced mathematics.

Rigor does have its proper place. In mathematics or formal logic—and these of course can enter into an economist’s work—one does not want lapses from due rigor; one does not tolerate either mistakes or steps in the argument where crude appeal to intuition substitutes for logical entailment.

Yet even in mathematics, excessive or premature insistence on rigor can impede progress (Lakatos 1976). Davis and Hersh identify a myth of totally rigorous and formalized mathematics (1986, section on “Mathematics and Rhetoric,” pp. 57-73). No one knows exactly what constitutes a mathematical proof. All proofs fall short of complete formal logic and so of commanding absolute confidence. A mathematical proof written in complete logical detail would be unreadable and incomprehensible. “Professedly rigorous proofs usually have holes that are covered over by intuition” (p. 69; an example follows). Proof simply means proof in enough detail to convince the intended audience. The competent mathematician knows where his audience should focus their skepticism. There he will supply sufficient detail, abbreviating the rest. Most mathematical articles, Davis and Hersh add, do not get close scrutiny from either referees or journal readers.

Garrett Hardin identifies such a thing as “mathematical machismo” (1986, p. 39). Arrogant numeracy can do harm. Lord Kelvin said, “[W]hen you cannot measure it in numbers, your knowledge is of a meagre and unsatisfactory kind” (quoted in Hardin 1986, p. 39). Yet Kelvin radically underestimated the age of the earth, predicted that man would never fly in craft heavier than air, and predicted that any metal cooled almost to absolute zero would become an electric insulator (p. 40). Many contributions to science, as by Darwin, Pasteur, Kekulé, Harvey, Virchow, Pavlov, and Sherrington, have been much more qualitative than quantitative (p. 41).

Even more so than mathematical proofs, knowledge of the real world simply cannot be totally rigorous; induction is not deduction.

In Karl Brunner’s view, the new-classical and “Minnesota” school of macroeconomics, with its insistence on beginning from the supposed beginning, commits what he called the “Cartesian fallacy.”

The Cartesian tradition insisted that all statements be derived from a small set of “first principles.” “Cogito ergo sum” and everything else follows... . Anything not derived from “first principles” does not count as knowledge. You are not allowed to talk about money if you have not derived from “first principles” a specification of all the items which are money. This methodological position is quite untenable and conflicts with the reality of our cognitive progress over history. Science rarely progresses by working “down from first principles”; it progresses and expands the other way. We begin with empirical regularities and go backward to more and more complicated hypotheses and theories. Adherence to the Cartesian principle would condemn science to stagnation. There are, moreover, as Karl Popper properly emphasized, no first principles. (Karl Brunner interviewed in Klamer 1983, p. 195; compare Brunner 1989, pp. 225-227.)

The Cartesian fallacy appears linked with what W.W. Bartley III (1984) called “justificationism.” An often unrecognized trait running through the history of philosophy, justificationism is the expectation that all propositions be justified (demonstrated, proved, warranted) by appeal to some authority, whether reason in the style of Descartes, empirical observation, divine revelation, or some other definitive source. But no interesting propositions can be justified in such a way. The demand for justification is a piece of ancient methodology carried forward uncritically into modern discussion (1984, p. 221 in particular). Bartley rejects justificationism in favor of the Popperian process of conjectures and refutations. Scientists invent laws and theories and devise ways of winnowing out wrong ones. It is reasonable to accept, tentatively, laws and theories not yet rejected on logical or empirical grounds and not yet displaced by more attractive alternatives. Accepting them in that way is not the same, however, as holding them to have been justified or proved; for positive justification is downright impossible. We cannot criticize all of our beliefs all at the same time. Criticism of particular propositions or theories must employ others—notably, standard logic—taken as valid for the purpose at hand. But none of these is exempt from criticism in all contexts. Although we cannot criticize everything at once, nothing is properly immune against any criticism in all circumstances and contexts. (See the many pages on justification and justificationism cited in the index to Bartley 1984.)

ANOTHER THEME: MODELS

Years ago a graduate-student advisee reported to me the expectations of another of his advisors: he must build his dissertation around a model.

“Why?” the student asked. “I don’t know,” was the reported reply, “you’ve just got to have a model.” The other advisor reportedly went on to say that if the student expected to get his dissertation past certain members of the department, he would have to do work of the kind they expected.

Such sermonizing seldom appears in print and fully articulated, which is why it can be so insidious. Although influential, it escapes critical examination. I wish economists would drag it into the open by recounting their experiences with it. (Mayer makes a good beginning in his 1993, chap. 9, entitled “Model or Die.”)

One little episode involved me directly. During the discussion period at a conference, I remarked that a particular monetary reform would eliminate the contagion of bank runs, and I briefly explained why. During the further discussion, and at greater length during the coffee break, another conferee objected that if I and my coauthor expected anyone to understand what we were saying, we would have to argue in the context of a model of bank runs, complete with specification of 100 persons, 47 commodities (or whatever the numbers might be), and so forth. If I had thought fast on my feet, I would have pressed the question “Why?”. I would have asked my interlocutor to make his methodological sermon explicit and support it with reasons. Unfortunately, the conversation wandered off.

Months later, in conversation with Donald McCloskey, I wondered about the claims of some economists not to understand arguments presented outside of formal models. McCloskey conjectured that they mean what they say: some of them are so wrapped up in their own models and favorite symbols that they actually cannot understand arguments presented in an unexpected language, English.

Peter N. Ireland (1994) provides another example of what bothers me. After making sensible remarks about relations between money and economic growth, he goes on to give his argument supposed rigor with mathematics and numerical simulations. He elaborates a model of a large number of identical, infinitely lived households possessing perfect foresight. Each consists of a worker and a shopper. Production functions have specific special properties. Perfect competition prevails. A cash-in-advance constraint applies to purchases made without the assistance of a financial intermediary. Yet if these and other special assumptions spelled out in great detail (about transactions costs and so forth) are not necessary for the conclusions reached, what is the point of making them? And if they are necessary, is it not a great lapse from the trumpeted rigor to convey the impression that the conclusions reached apply to the messy real world anyway?

In the same journal issue, Steve Williamson and Randall Wright (1994) explain how money, besides providing its familiar services, cuts down the information requirements of exchange, giving transactors a better chance than they would have under barter to wind up with high-quality goods. The authors’ model assumes away the noninformational difficulties of barter, leaving no role for money in the absence of private information. Time is discrete and goes on forever. The population is a continuum of immortal agents who can produce both good and bad commodities at positive and zero utility cost, respectively. Consumption of money, of a bad commodity, or of one’s own output yields zero utility, while consumption of someone else’s good output does yield utility. Detailed assumptions about proportions of good and bad commodities, probabilities of encounters, and so forth create the opportunity for numerous equations and graphs adding nothing to the central message, as far as I can see, except spurious rigor. The authors give no reason for supposing that what is rigorously true of their concocted world is equally true of the real world.

Robert Frank has done much insightful writing at the intersection of economics, psychology, and ethics. His article of 1987, however, provides an example of the merely decorative use of mathematical code, as distinguished from bona fide manipulation requiring symbols. One footnote (1987, p. 595) even promises “a more reader-friendly version” of his model in a then-forthcoming book. Well, why wasn’t he friendly to his current readers? Bénassy’s article of 1993, which I admire for its actual substance, is similarly discourteous in its use of symbols. Bénassy actually distinguishes between certain concepts by whether the identical double-subscripted letters representing them are topped by a macron or by an only slightly wavy tilde; this is a subtlety likely to escape a reader not wielding a magnifying glass. I suspect that he, like Frank, Ireland, and Williamson and Wright, was bowing to tacit methodological pressures.

As Mayer’s strongest-link (or most-rigorous-link) principle suggests, a display of technique can plaster over much. Robert Solow was staying within the bounds of permissible exaggeration when he wrote (1985, p. 330) that a modern economist, dropped with his computer from a time machine into any old time and place, will soon

have maximized a familiar-looking present-value integral, made a few familiar log-linear approximations, and run the obligatory familiar regression. The familiar coefficients will be poorly determined, but about one-twentieth of them will be significant at the 5 percent level, and the other nineteen do not have to be published. With a little judicious selection here and there, it will turn out that your data are just barely consistent with your thesis adviser’s hypothesis ... , modulo an information asymmetry, any old information asymmetry, don’t worry, you’ll think of one.

Walter Eucken (1948, Pt. 11, esp. pp. 192-193) criticized two rather opposite trends in theory. Often the question is asked how things would go in an a priori model built with little reference to reality. The very framing of the question excludes reality. On the other hand, Eucken continues, analysis may work with crude, sweeping concepts like “capitalism,” “laissez faire,” or “socialism.” But both a priori models and imprecise “blanket” concepts can be of little help in investigating reality.

James Tobin (1980, p. 86) comments on overlapping-generations models of money. Long before, economists had already pointed out how a common medium of payment facilitates multilateral trade, whereas barter would restrict transactions.

The insight tells us why the social institution of money has been observed throughout history even in primitive societies. An insight is not a model, and it does not satisfy the trained scholarly consciences of modern theorists who require that all values be rooted, explicitly and mathematically, in the market valuations of maximizing agents. But I must say in all irreverent candor that as yet I do not feel significantly better enlightened than by the traditional insight.

Let me quote two physicists. Pierre Duhem (1954, esp. chap. iv) does not deny the usefulness of models. He recommends “intellectual liberalism.” “Discovery is not subject to any fixed rule... . The best means of promoting the development of science is to permit each form of intellect to develop itself by following its own laws and realizing fully its type” (1954, pp. 98-99). Duhem questions the claim that providing a “mechanical or algebraic model” for each of the chapters of physics satisfies all the legitimate wishes of understanding (p. 100). Perhaps the most fruitful procedure in physics has been the search for analogies between distinct categories of phenomena, but we should not confuse it with modeling (pp. 95-97). The use of mechanical models “has not brought to the progress of physics that rich contribution boasted for it.” Its contribution “seems quite meager when we compare it with the opulent conquests of abstract theories. The distinguished physicists who have recommended the use of models have used it [that method] far less as a means of discovery than as a method of exposition” (p. 99).

Ronald Giere (1988, esp. chap. 3, “Models and Theories”) describes models as stylizations or idealizations about which propositions hold more rigorously true than they ever could about their possible counterparts in reality (cf. Hausman 1992, pp. 75-82, 273). F= ma and other general “laws” of mechanics are not really empirical claims but more like general Schemas that need to be filled in (Giere 1988, p. 76). If the laws of motion, such as the law of the pendulum, were to give a literally true and exact description of even the simplest of physical phenomena, they would have to be incredibly more complex than any that could ever be written down. The nonuniformity of gravity near the earth’s surface, the gravitational force of the moon, nonlinearities in air resistance, and so forth would all have to be taken into account. Idealization and approximation are of the essence of empirical science (pp. 76-78). Hooke’s law “states that the force exerted by a spring is proportional to the amount it is stretched,” the constant of proportionality being “interpreted as a measure of the stiffness of the spring” (p. 68). Such a statement presupposes certain “idealizations,” such as that the spring is without mass and subject to no frictional forces, that the force-displacement is linear, that the attached mass is subject to no frictional forces, and that the wall is rigid, so the wall recoil due to motion of the mass maybe neglected (Giere, pp. 69-70). In mechanics, “The equations truly describe the model because the model is defined as something that exactly satisfies the equations” (p. 79). (The physicist Henri Poincaré repeatedly insisted on similar points about the role of stylizations and conventions in science; see Yeager 1994, esp. pp. 161-162, and Poincaré’s writings cited there.)

Unlike a model, a theoretical hypothesis is ... a statement asserting some sort of relationship between a model and a designated real system (or class of real systems)... . The general form of a theoretical hypothesis is thus: Such-and-such identifiable real system is similar to a designated model in indicated respects and degrees. (Giere 1988, pp. 80-81)

Lucas and Sargent (1978, p. 52) say in effect that anyone uttering any proposition of economics must, whether he realizes it or not, be working with some sort of model in mind. It may be vague or clear, poor or good; but if the economist does not set forth his model explicitly, he is just hiding it from professional scrutiny and criticism.

Is it true, though, that one is necessarily working with a model? If the term “model” is stretched to cover any piece of reasoning, then it seems a mere equivocation to insist after all on a model in a narrower sense. If “model” means a complete set of equations specific enough to be ready for econometric estimation, the answer is pretty clearly that the theorist is not necessarily working with one. He may not want to restrict himself to any specific model because he believes that suitable ones differ widely in their details across times and places. Consider a model of our solar system. For some purposes we are interested in the system’s specific, historically accidental, features; and for such purposes, a detailed model is necessary. But for other purposes we want to emphasize propositions of wider application, such as those of gravity; and then it would be pointless to be tied down to a model of a particular solar system.

Similarly in economics, propositions of the sort we hope to develop may not pertain to an economic system of one specific structure; and then a specific model maybe mere clutter. As Ludwig von Mises once remarked (orally) about an econometric investigation of the watermelon market, none of the fundamental propositions of economics depends on the existence of such a commodity as watermelons. Nor, one might add, does any depend on the existence of such a country as the United States of America.

In many contexts, by the same token, we are concerned with propositions applicable widely enough not to stand or fall on the existence of railroads or labor unions or negotiable certificates of deposit. What sort of model it may be legitimate to insist on, if on any at all, thus depends on the purpose at hand, including the conceived scope of the propositions under investigation.

The investigator might recognize that he cannot produce a mathematical or econometric model with specific details yet wide applicability. He might be concerned, instead, with the characteristics that any plausibly relevant model would have—if one insists on speaking of models. He might be seeking Bauer’s “propositions of generality and depth.” Examples in economics include the principle of diminishing marginal returns, the law of demand, and the quantity theory of money. They enter into the construction of widely different specific models. The investigator might legitimately be more concerned with such propositions themselves than with one or another of their particular embodiments. Before one can sensibly construct a model, one must have some idea of what observed or conjectured or even merely postulated features of reality one is trying to embody in it. One needs to know what relations of interdependence or cause and effect one is trying to exhibit. In that sense, propositions (and the concepts they employ) are logically prior to models. (Kosko 1993, pp. 165, 169, 177, makes sensible remarks about models and about the frequent usefulness of “model-free estimation or approximation” and “model freedom.”)

Far be it from me to taboo modeling, which can be a way of stimulating, organizing, and presenting one’s thoughts.⁶ A burst of insistence on modeling may even be justified if it is provoked by someone’s argument that is too vague, is phrased in idiosyncratic language, or rests on unstated assumptions. If so, challenging the theorist to put his argument into graphs or equations may force him to make his assumptions and reasoning explicit. More generally, translating an argument from one style into another may serve as a check on one’s reasoning and improve communication. (Thomas Hobbes made a noteworthy case for the translation test in 1651/1968, chaps. 8 and 46.) While translation can indeed be beneficial, the logical priority of propositions over models embodying them casts doubt on insistence on modeling as the only legitimate way to develop and communicate propositions. What warrant, then, does a critic have for accusing an investigator of doing something disreputably cryptic—namely, working with a model while protecting it from inspection—when he may not be working at the modeling stage at all?

ECONOMETRIC EVIDENCE

The recent vogue of real-business-cycle models has produced econometric studies purportedly discrediting the more traditional focus on money as a source of business fluctuations. Econometric studies enjoy the recommendations of explicit and tacit methodology both. They enjoy the reputation of coming to grips with reality by high-powered techniques, in contrast with commonplace and mostly qualitative observations of the role of money over the centuries and throughout the world and also in contrast with questions about the nature of the barriers in the channels through which money plausibly would affect output.

An article by Hansen and Prescott (1993) provides a partial exception to the observation that real-business-cycle theorists do not identify the “real” shocks that their theory presupposes. Ultimately, though, the partial nature of that exception supports the observation. Without explicitly saying so, Hansen and Prescott convey the impression that they are answering “yes” to the question posed by their title, “Did Technology Shocks Cause the 1990-1991 Recession?”, thus invoking that episode in support of their theory. In their concluding paragraph (p. 286) they say: “Of course, if technology shocks continue to be above average, the United States will experience a boom; if the shocks in the coming year are below average, we can expect a recession.” Earlier (e.g., p. 284), they say that their model economy had a recession roughly matching that of the actual economy in timing, magnitude, and duration.

Hansen and Prescott’s method was to construct a model economy, modified from the standard real-business-cycle model and calibrated with figures from the real world. They calculate supposed productivity or technology parameters from employment data and other macroeconomic figures. They find that fluctuations of the model and actual economies match each other fairly well, except for stronger and more rapid reactions to productivity shocks and faster recovery from the recession in the model than in the real world. (Robert Clower’s “major objection to the new classical economics,” comes to mind: “it equates theoretical progress with improved econometric performance of theoretical models rather than with enhanced understanding of the way in which decentralized economic systems work.” 1984, p. 272.)

Lacking space to describe their procedures in detail, Hansen and Prescott nevertheless convey the impression that sophisticated technique went into reaching their results, as if that very fact recommends them. Despite entitling one section “What Are These Technology Shocks?” (pp. 280-282), the authors do not actually name the supposed causes of recession. At most they hint that antipollution regulations may have been involved. This style of exposition—conveying impressions rather than mustering explicit evidence and argument—requires comment that I nevertheless refrain from providing here, except to point out an example of tacit cheerleaders for rigor arguing in quite a nonrigorous way.

Philip Cagan reviews studies that manage to avoid detecting the influence of monetary changes on output (1989, followed by comments by Robert Rasche and others). Cagan criticizes the regression techniques commonly employed, “Granger-causality” tests, and particularly vector-autoregression studies, for the way they handle correlations among the “independent” variables, because of processing of the data (prewhitening, trend removal, and other purifications of time-series data in ways that throw away some of the association that may exist), and because these methods are testing for specific (e.g., linear or log-linear) relations and rigid relations among the variables, whereas money exerts its effects with “long and variable lags.” The filtering techniques employed remove much of the cyclical movements in money, and monetary influences are masked by innovations in interest rates, in turn reflecting monetary policy. (Michael Bordo, editor of the volume, adds that observation.) The VAR technique for dealing with spurious correlation eliminates important monetary changes. By removing all serial and cross correlations from economic series, VAR in effect removes all but short-run blips in money, losing the influence of relatively sustained monetary changes that do tend to affect business activity.

Cagan also criticizes the treatment of money’s endogeneity. (Monetarists know that connections between monetary changes and business activity can run and evidently have run in both directions.) If the Federal Reserve could override the endogeneity of money and thereby make output behave differently than it behaves in fact, then money does count. There is a difference between being endogenous with no independent effect and a mutual dependence which policy can affect. Those who deny monetary effects on output may be aware of this point but continue to neglect it. Even if money had been in some sense completely endogenous in 1929-1933, the Federal Reserve could have overridden that endogeneity and saved the economy from devastation.

I can only raise, not answer, a few further questions about supposed econometric evidence. Is it really informative to run correlations with time-series figures taken not only from periods of cyclical or “abnormal” change in output, money, prices, and so forth but also from periods of steadiness or relatively steady growth (or relatively undisturbed money-supply-and-demand relations), as if all these figures, taken indiscriminately, constituted observations on a single universe? In other words, can one really examine and compare the effects of monetary and nonmonetary disturbances by jumbling together numbers from periods both experiencing and not experiencing such disturbances? The issue is not really what calculated parameters describe ill-defined average-over-time relations among various macroeconomic variables. The issue, instead, is the how the phenomena of recession and recovery maybe causally related to contemporaneous and earlier events.⁷

If one would rather not find or see something—like monetary disturbances and their consequences—ways are available. The story comes to mind of Admiral Nelson putting his telescope to his blind eye at the battle of Copenhagen.

More fundamentally, what reason is there to suppose that a definite “structure” of the economy, describable by definite functions and definite coefficients, exists in the first place as an object amenable to econometric investigation? Furthermore, even if a mathematically formulated system were deterministic, with known and fixed parameters, the simplest kinds of nonlinearity could render even its qualitative behavior after several or many “rounds” extremely sensitive to parameter sizes and initial conditions. Still further, the real system being modeled, instead of being isolated, is exposed to innumerable perturbations (including “noneconomic” ones) that in principle require being taken into account. In such a system, numerical prediction is impossible (except, perhaps, for short-run extrapolation); the best that can be done is qualitative prediction, or recognition of patterns. Similar remarks apply to attempts to characterize the “processes” supposedly at work in real economies—whether or not they have unit roots, and so forth.

These are among the lessons for economics of the recently popular mathematical theory of “chaos” or “catastrophe.” (See Ekeland 1988, who brings E.N. Lorenz’s “butterfly effect” and Henri Poincaré’s reservations about quantitative modeling into the story.) I do not want to be misunderstood, however, as issuing methodological taboos of my own. Econometric research into recent or earlier economic history can indeed be informative, and its techniques are worth cultivating for applications outside as well as within economics. I merely want to question insistence on them as both obligatory and decisive across practically the whole broad range of economics. Especially where human action is the subject matter, much can be said for observations described and reasoning conducted largely in the terms that people themselves use when they perceive and think about and cope with reality.

EVIDENCE OF OTHER KINDS

Cheerleaders for rigor tacitly imply that only numbers constitute really respectable evidence. Everything else is anecdote; and, in the economist’s quip, “a historian is one who believes that the plural of anecdote is data” (Brennan and Lomasky 1993, p. 90). Yet Brennan and Lomasky, undeterred, deny

that the world is describable exhaustively by numbers or that broad brush descriptions of the political landscape have nothing of relevance to contribute to the collection of evidence... Anecdote does ... have a role to play, and a good feel for the whole story is a crucial prerequisite for proper empirical judgment... More than “fitting the facts” is required of a theory; it must also genuinely explain, in the sense of rendering intelligible, the facts it fits. (1993, pp. 90-91; compare Higgs 1987, pp. 31-32)

The history of science shows, with Copernicus and Darwin as examples, that theory can play a powerful role in organizing understanding even before it can provide quantitative predictions. The Wealth of Nations contains little quantitative detail but had great impact “as a way of seeing how things fit together qualitatively.” Quantitative prediction, though a reasonable goal for science, is not the test of a new theory (Margolis 1982, pp. 10-11).

If an economist is not willing to analyze nonquantitative evidence such as executive orders, statutes, court decisions, and regulatory directives, writes Robert Higgs (1987, p. 32), then perhaps he should abandon

his pretensions in this field of study... The keys lost elsewhere will never be found under the lamp post, not even with the aid of the most powerful floodlights. The spectacle of economists bringing their awesome mathematical and statistical techniques to bear on the analysis of irrelevant or misleading data can only disgust those for whom the desire to understand reality takes precedence over the desire to impress their colleagues with analytical pyrotechnics.⁸

Robin Winks collected several historical essays under a suggestive title, The Historian as Detective (1969). Like a detective trying to solve a murder case, a good researcher of historical questions does not let methodological prejudice or intimidation⁹ narrow the range of kinds of clues he is willing to sift. He is willing to undertake episode-by-episode analysis, or any other kind that appears promising. Economists, we may hope, will become equally open-minded even about novel evidence and argument.

COMPETING HYPOTHESES

The disparagers of money-oriented macroeconomics take few pains to link up their theories with earlier theories and the facts that they appeared to account for. (Yet in the natural sciences this is standard practice. Kepler’s astronomy accounted for the observations that the Ptolemaic theory had already accommodated. Einstein’s relativistic mechanics assimilates Newtonian mechanics as giving an excellent account of a special case, which happens to be the world of ordinary human observation.) Instead, the disparagers of money continue tinkering with their “real” models, “calibrating” them, ingeniously striving for verisimilitude.

So doing, they disregard or flout the method of multiple competing hypotheses. Actually, this is not a specific method or technique, nor is it a tissue of methodological exhortations and taboos; rather, it is a broad approach or attitude toward research. The biophysicist John R. Piatt (1964), echoing and reinforcing the geologist T.C. Chamberlin (1897/n.d.), persuasively argues for developing rival hypotheses and seeking ways to rule each one out, seeing which one or more, if any, stand up to the challenges of the best evidence obtainable.

The contrasting approach or attitude is simply to seek arguments and evidence in defense of one’s own favorite hypothesis. “[I]n numerous areas that we call science,” Piatt observes (p. 352), “we have come to like our habitual ways, and our studies that can be continued indefinitely. We measure, we define, we compute, we analyze, but we do not exclude. And this is not the way to use our minds most effectively or to make the fastest progress in solving scientific questions.” A researcher with a parental affection for his own favorite theory, Chamberlin had already observed (1897/n.d., p. 840), searches especially for phenomena that support it. Unwittingly he presses the theory and the facts to fit each other.

Chamberlin in effect advocated substituting discussion for debate. The two are different in spirit. The debater seeks the decision of the judges for his already adopted conclusion; a discussant searches for truth (F.A. Harper in a “publisher’s note” to the reprint of Chamberlin’s article). “The conflict and exclusion of alternatives that is necessary to sharp inductive inference has been all too often a conflict between men, each with his single Ruling Theory. But whenever each man begins to have multiple working hypotheses, it becomes purely a conflict between ideas. It becomes much easier then for each of us to aim every day at conclusive disproofs—at strong inference—without either reluctance or combativeness.” Researchers become excited at seeing how the detective story will turn out (Piatt 1964, p. 350).¹⁰

The foregoing views require qualification. Not every researcher need be testing several hypotheses. Division of labor can be fruitful. Some researchers may legitimately work to give one particular hypothesis its best possible shot. It may be instructive for themselves and others to see what persistence and ingenuity can do toward salvaging even a hypothesis that does indeed seem preposterous on its face. Furthermore, some may flourish in a setting and incentive structure of rivalry not merely among ideas but among persons. Differences not merely of abilities, training, and interests but even of temperaments maybe put to good use. But to the extent that some economists do work ingeniously at protecting their favorite theories, the task falls all the more to others to perform the necessary confrontations.

Not only real-business-cycle theorists but monetarists must face the objections voiced by Chamberlin and Piatt. Still, monetarism is not irrefutable in the disreputable sense of enjoying built-in protection against any adverse evidence. Observations are readily conceivable that would indeed refute it. If these are merely conceivable, not actual, and if they would run counter to manifest facts about the role of money in the everyday activities of individuals and business firms, well, a theory is scarcely at fault for recognizing those facts.

The method of competing multiple hypotheses scarcely requires that no question ever be settled, not even tentatively, and that multiple hypotheses always remain in active contention on all topics. It would be no scandal if a strong consensus eventually developed on the monetary (or nonmonetary) nature of business cycles. What would be a scientific scandal would be to grant certain questions perpetual immunity to ever being reopened, no matter what new evidence and lines of reasoning might be developed.

FALLACY-MONGERING

Countermethodology, which I distinguish favorably from methodology, does not mean that “anything goes.” It in no way exempts any argument or supposed evidence from critical inspection. Critics should point out specific defects, however,—slips in logic and errors of fact—rather than just sneer broadly at the use of some methods but not others.

Despite Donald McCloskey’s lack of enthusiasm for what he calls “fallacy-mongering” (1985, pp. 48-49), it can be useful to identify and classify specific types of unsatisfactory argument. McCloskey is emphatically in favor of scholarly dialogue, conversation, or rhetoric. Well, dialogue consists largely of critical examination of arguments and evidence and supposed inferences, and being acquainted with and alert to frequent types of fallacy can help in this examination. McCloskey himself warns against some particular types, such as confusion between statistical significance and substantive significance of coefficients in fitted equations (1986; also 1992, p. 267). Identifying and categorizing fallacies is not at all the same thing as issuing methodological injunctions and taboos. Rather, it resembles the bottom-level, nuts-and-bolts methodology acceptable to McCloskey.

Now, what are some types of fallacy—and, to broaden our target, types of irrelevance—found in economic discourse?

• Standard fallacies that textbooks warn against, such as the fallacy of composition (and reverse fallacies of composition).

• The Ricardian Vice (so called by Schumpeter 1954, pp. 668,1171): “the habit of establishing simple relations between aggregates that then acquire a spurious halo of causal importance, whereas all the really important (and, unfortunately, complicated) things are being bundled away in or behind these aggregates,” in other words, “the habit of piling a heavy load of practical conclusions upon a tenuous groundwork, which was unequal to it yet seemed in its simplicity not only attractive but also convincing.”

• “Austrian-style disquisitions on the foundations of human knowledge and conduct and the like,” an irrelevancy characteristic of Frank Knight’s writings, according to LeRoy and Singell (1987, p. 402).

• Similarly, nonsubstantive brooding over the meanings of concepts, as over the essence of entrepreneurship.

• Assuming constancy of magnitudes that simply cannot remain constant in the face of changes in other magnitudes considered (Buchanan 1958).

• Failure to distinguish between individual and overall points of view or, relatedly, failure to make, when relevant, Patinkin’s distinction between individual experiments and market experiments (1965, chap. 1 and appendix).

• Failures to distinguish when necessary between actual and desired changes in holdings of money, between an excess demand for or supply of home money on the foreign-exchange market and an excess demand for or supply of domestic cash balances, and between demand for assets denominated in a particular currency and the demand for holdings of that currency as a medium of exchange.

• The real-bills fallacy, which keeps turning up in new disguises.

• Tacitly supposing that lack of tight short-run correlation between changes in certain magnitudes discredits the broad relation that standard theory indicates between their levels. (Nowadays the technique of cointegration is cultivated as a means of overcoming this fallacy.)

• Mere eloquence that crowds out quantitative considerations. Hardin duly condemns decisions dominated by sheer eloquence, whereas the numerate outlook shows a concern for how big, how important, phenomena and effects are (1986, esp. pp. 42-44).

ATTITUDES AND PRESSURES

Fritz Machlup (1956/1978, chap. 13) listed several signs of an “inferiority complex of the social sciences,” including Behaviorism, Operationism, Metromania, Predictionism, Experimentomania, and Mathematosis. Pressure to resemble the physical sciences does seem to be a kind of tacit methodologizing.

Another, apparently, is attunement to fads.

In science, as everywhere else, there are few true creators, people able to leave the beaten track and to come up with new ideas. It is very tempting to deem a problem interesting because half the people you know are working on it. But truly deep and difficult problems promise no easy returns, and do not attract people eager to publish. Poincaré makes a distinction between problems that nature sets up and problems that one sets up (Ekeland 1988, p. 25).

What one might call frontiersmanship is a related attitude. Conjecturably it tends to crowd out due attention to history, both of subject matter and of research and doctrine in one’s field. In macroeconomics, older and more straightforward doctrines, whatever their merits, were, well, remote from the frontier. Other fields appeared more suitable for the academic game. On the supposed frontier, business-cycle researchers, whether belonging to the new-classical or the “real” school, tend to neglect historical episodes helping to support (or to discredit) the monetarist explanation of cycles. They also neglect or slight the fact that competent observers in widely diverse times and places saw reason to be persuaded of the monetary nature of cycles. Yet this widespread perception surely counts for something, especially since it does not stand alone but complements a variety of other evidence.

Also at work in contemporary macroeconomics is an attitude that I do not want to label; it can exhibit itself. Referring to New Keynesian economics in particular (which, being mislabeled, has close though inadequately appreciated affinities with monetarism), Robert G. King mentions macroeconomists working “on the banks of the Charles River,” whose product he disparages in contrast with “that of macroeconomists at the universities where the cutting-edge research has been done over the past decade.” The latter consists of dynamic general equilibrium microeconomic models of macroeconomic phenomena. “It is what most graduate students are now learning and what most undergraduates will soon learn. In two decades or less, it will be hard to find a macroeconomist whose first reactions to policy problems will not be conditioned by sustained exposure to [it]” (King 1990, p. 162). In a later article, King reproaches New Keynesians for attempts at “marketing” a version of macroeconomics resembling a Ford Pinto. “The danger is that macroeconomists and policy-makers will pay too much attention to the new Keynesian advertising, and assume for too long that the old product is a sound one” (King 1993, concluding sentence).

ACADEMIC INCENTIVES AND GAMES

The state of academic economics is far from wholly bad; progress does occur. Critics, though, see grounds for complaint. An article chosen at random out of any economics journal, James Buchanan finds, is unlikely “to have a social productivity greater than zero. Most modern economists are simply doing what other economists are doing while living off a form of dole that will simply not stand critical scrutiny” (1979, pp. 90-91). More recently a young academic superstar has said much the same:

In America’s academic system, professors of economics get tenure and build reputations that give them other academic perks by publishing, and so they publish immense amounts—thousands of papers each year, in scores of obscure journals. Most of those papers aren’t worth reading, and many of them are pretty much impossible to read in any case, because they are loaded with dense mathematics and denser jargon. (Krugman 1994, p. 8)

“Academic programs almost everywhere,” Buchanan continues, “are controlled by rent-recipients who simply try to ape the mainstream work of their peers in the discipline” (Buchanan 1983/1988, p. 130). Mainstream economists of the 1950s, though wrong on much, were interested in ideas, Buchanan says, and were not frauds or conscious parasites. Since then economics has become

a science without ultimate purpose or meaning. It has allowed itself to become captive of the technical tools that it employs without keeping track of just what it is that the tools are to be used for. In a very real sense the economists of the 1980s are illiterate in basic principles of their own discipline... .Their interest lies in the purely intellectual properties of the models with which they work, and they seem to get their kicks from the discovery of proofs of propositions relevant only to their own fantasy lands. (1983/1988, pp. 126-127)

Maurice Allais, a mathematical economist who won the Nobel Prize two years after Buchanan did, shares his skepticism. For almost forty-five years, Allais said in 1989, economic literature has featured “completely artificial mathematical models detached from reality.” Allais recommends mathematics to economists not for its own sake “but as a means of exploring and analyzing concrete reality.” When neither a theory nor its implications “can be confronted with the real world, that theory is devoid of any scientific interest.”

In a broader context, Garrett Hardin (1986, pp. 175-176) observes an information glut. “A substantial and growing proportion of the scientific literature is pure jam [in the sense of traffic jam], the consequence of egotistic scientists putting out multiple, repetitive publications in an effort to be noticed... .Progress is impeded. Society suffers.” Referring to the examination system for the Mandarins of imperial China, Michael Walzer (1983, p. 141) notes that “examiners increasingly stressed memorization, philology, and calligraphy, and candidates paid more attention to old examination questions than to the meaning of the old books. What was tested, increasingly, was the ability to take a test.” In today’s academic world, similarly, what gets rewarded seems to be the ability to get rewarded.

Without charging specific individuals with misconduct or reprehensible motives, we may remind ourselves about gamesmanship. Occasionally the writer of an article will try to butter up prospective referees or otherwise engage in politicking to get it published.¹¹ What is more relevant to our topic, writers sometimes put on a display of erudition, using techniques more advanced than are helpful,¹² otherwise parading supposed rigor, making forays into other academic disciplines, or citing scarcely relevant but impressively obscure sources. Some of this gamesmanship is no doubt tolerable: even serious researchers are entitled to a little fun. It does little damage when it is evident for what it is. It is less tolerable, however, when it warps the writer’s approach to the subject matter and his or his readers’ understanding.

This situation traces partly to the incentive structure in academe. We observe something reminiscent of the role of “success indicators” in the Soviet command economy. Meeting the target, satisfying the criteria, becomes the objective, crowding out attention to the wants of the customers or—in the present context—the advancement of knowledge, the pleasure of the quest, and the enlightenment of readers and students. The blame falls partly on administrators desiring easy-to-administer criteria for tenure and promotion. As I have observed on committees and otherwise, some evaluators focus not on the actual merits of scholarly work but on the supposed prestige of the journals where it appeared, a consideration related in turn to attunement to fads and fashions. The “second-handism” duly condemned by Ayn Rand rides high (see the passages from her works reprinted in Binswanger 1986, pp. 438-441).

Something may well be said for “schools,” which can encourage a researcher with the prospect of a sympathetic audience. But a school influential enough to dominate what are considered to be success indicators can have a baneful influence, inhibiting independent thought.

THE MARKET ANALOGY

Sometimes second-handers try to justify their stance by invoking the free market in goods and services. Once, when the board of directors of the Southern Economic Association was discussing whether to nominate a particular economist for some position or other, a member whom I’ll identify only as “TS” said in effect: “It doesn’t matter what we here think of his work; let the market decide.” TS went on to name the journals that had printed the candidate’s work. At least two things were wrong with this appeal to “the market.” First, the ultimate consumer, the reader of academic journals—or, more exactly, the subscriber—has an influence more attenuated and more subject to manipulation by others than the influence of the consumer of ordinary consumer goods and services. Editors and referees have reason and scope for heeding fads and cliquish and personal considerations. They are not risking their own money. Subscribers face tie-in sales (which include association memberships and the supposed prestige of subscribing) and have reason, anyway, to learn about fads, whether they like them or not. It is harder in the supposed academic market than in the real market for customers to know whether they got what they paid for.

Second, since when was the market, even the actual business market, supposed to be the arbiter of excellence in literature, art, music, science, or scholarship? Since when does it decide truth and beauty? The case for the free market is something quite other than that it constitutes the very criterion of what should be admired, and it ill serves the cause of a free society to misrepresent the case for the market.

Finally, TS’s position is the very prototype of the second-handism diagnosed by Ayn Rand. Misbehavior in the “marketplace” for ideas is worse than in the marketplace of goods, suggests W.W. Bartley III, because few penalties against offenders are readily enforceable, while “whistle-blowers” are severely punished (1990, chaps. 6 and 7; the analogy between the academic and business markets is further dissected in Mirowsky 1992, pp. 239, 247, and Mayer 1993, pp. 10ff, 84).

CLARITY VERSUS OBSCURANTISM

Overcoming tacit methodological preachments requires, for one thing, cultivating clarity. An article by Max Eastman (1929/1940) is worth citing if only for its insightful title, “The Cult of Unintelligibility.” That label fits not only Eastman’s specific target, “modernist” poetry, but much academic activity. Yet contempt for conveying a clear message violates the spirit of science, which “is nothing but a persistent and organized effort to talk sense” (Eastman 1929/1940, p. 366). Bartley found the obscurantism of certain entrenched ideologies occurring in two main forms, inappropriate mathematical formalism and lack of clarity in speech and presentation (1990, pp. I32ff). As Karl Popper taught, pretentiousness is immoral (Bartley 1990, p. 159). Popper would “always try to dislodge his conversational partners from any habits or tricks that preserve their ability to impress and dominate, and to maintain the pretence of knowledge they do not possess” (Bartley 1990, p. 265).

Authors of books on grammar and writing style do not hesitate to warn their readers about specific errors and stylistic infelicities. In that connection, we do well to remember McCloskey’s top level of methodology, the ethics of scholarly discourse. Scientists are supposed to be engaged in an interpersonal endeavor, which includes, as McCloskey says, “conversation.”

Well, then, communicate. Do not pervert communication into parading how much you know of mathematics or the philosophy of science or whatever. Instead of striving to impress your reader, be polite to him. Edit; rewrite. Recognize that the form in which your ideas originally occurred to you may not be the most effective way to put them across. Do not suppose that employing symbols automatically confers a papal dispensation from obligations incumbent on any writer.

The offenses I have in mind include writing in code, with symbols replacing words, using symbols defined only haphazardly, omitting meaningful labels from diagrams, and using cryptic expressions with variable meanings (such as “real exchange rate” or “appreciation of the exchange rate”). Perhaps your reader can break your code; perhaps he should be able to figure out your argument even in its original, unedited form. But why should he have to bother? He feels more comfortable with occasional reassurances that you and he are on the same wavelength. After all, you might be making a mistake. I recall places where the writer used a slightly different symbol in a diagram than in the text, such as a lower-case instead of upper-case letter or a curved letter l instead of a straight one. Did the writer intend a distinction, and if so, what was it, or was he simply being careless? Such time-consuming puzzles could be avoided if the writer deigned to write clearly in the first place, perhaps even labeling his diagrams in English.

The central fact of economics is scarcity. Your readers’ time is scarce, as well as their capacity for attention and effort. Besides figuring your message out, they have other things to do. Many topics within and outside of economics besides your current message are worth their attention, and your own. (As Wilhelm Röpke used to say, economics is a subject in which understanding a part presupposes understanding the whole, and indeed more. An economist who is only an economist cannot even be a good economist.)

Remember that the principle of diminishing marginal returns applies widely, even to time and effort spent on a particular activity or topic. Even for readers who can follow an analysis, unnecessary formalist decorations often consume time that might have had other and better uses (Mayer 1993, p. 78). The principle of portfolio diversification applies not only to investment assets but also to knowledge of topics within and outside of economics.

Encouragingly, the mathematician Paul Halmos similarly exhorts his colleagues. They should write correct and clear English, keeping Fowler, Roget, and Webster at hand. A writer who works eight hours to save five minutes for each of 1000 readers saves over eighty man-hours. Halmos warns that the symbolism of formal logic, though sometimes indispensable, is a cumbersome way of transmitting ideas. Nobody thinks in symbols. Coding by the author and decoding by the reader waste the time of both and obstruct understanding. “The best notation is no notation,” Halmos advises. Try to write a mathematical exposition as you would speak it. “Pretend that you are explaining the subject to a friend on a long walk in the woods, with no paper available; fall back on symbolism only when it is really necessary” (Halmos 1973/1981, p. 40). Avoid distracting your reader with irrelevant labels (for example, referring to “the function f” when you will not be using the label f again). When conveniently possible, avoid coining new technical terms. Take care about the appearance of the printed page. Solid prose will have a forbidding, sermony aspect; “a page full of symbols ... will have a frightening, complicated aspect” (p. 44).

It maybe that clarity does not pay. (It costs time, but editors and referees have an opportunity to impose discipline on authors in the interest of the wider scholarly community.) Putting heavy demands on your reader may advertise your own learning. It may intimidate him into not questioning your argument. (Mayer 1993, p. 78, suggests that formalist trappings may help protect a paper from criticism by making critical comment on it costly in time and effort.) You may make your message appear fresher and more important than it really is by practicing product differentiation, as opposed to taking care to relate your message to the existing literature, exploiting similarities, parallels, analogies, and contrasts. Perhaps reconditeness and obscurity really do bamboozle editors and readers; and perhaps unintelligibility masquerading as profundity may sometimes ward off identification of what is no more than poor style. If so, a moral aspect enters into writing. (Cf. McCloskey 1986, writing in a slightly different context.) If so, furthermore, questions again arise about the incentive structure prevailing in academia.

At the very least, get your grammar, word usage, spelling, and punctuation right. (Nobody is infallible, certainly not I, but at least one should work at these things.) Why do economists tolerate so much slovenliness in these respects? They do not tolerate its counterpart in the mathematical strands of economics—not, that is, when they notice it (and I have some stories to tell about this qualification). If rigor is prized, why shouldn’t it be prized in the cut-and-dried aspects of writing?

If for some reason you cannot get your grammar and so forth right, then hire someone to repair your writing before you ship it off to a journal and perhaps even before you inflict it on colleagues. Beyond getting the mechanics right, strive for a readable style. When you ship your manuscript off to a publisher, have it in a form in which you would be glad to see it in print. Don’t count on someone else to improve it.

These exhortations bear on what to do about a national crisis (permit me to exaggerate as Andy Rooney does on the tube). Not even Walter Block, who wrote a whole book (1976) trying to portray the pimp, the drug pusher, the litterbug, and other unsavory types as heroes—not even he attempted any defense of the itchy-fingered copyeditor. That would have been just too preposterous. I wonder whether obscurities, jargon, and symbols may not sometimes help protect authors from tampering: copyeditors may shy away from trying to improve on manuscripts that they cannot even understand. Mere palpable sloppiness, on the other hand, flags the copyeditors on. One of my bitterest complaints against writers who think it beneath them to bother with their grammar, spelling, punctuation, and style is that they create externalities: they inflict the curse of copyediting even onto writers more careful than themselves.

Ideally, the author himself should be known to bear responsibility for what appears in print. If the writing is excessively bad, the publisher should simply reject it. As things now stand, however, sloppy writers provide an excuse of sorts for not straightforwardly solving the copyeditor problem.

CONCLUSION

I hope we are giving each other, and perhaps our students and readers, some moral support, some backbone, so that we can carry on our work in the ways that we ourselves think best suited for learning how the world actually operates. I hope we can carry on despite fads, fashions, perverse success indicators, and preachments about “rigor.” I hope we will have the courage to unmask and, when appropriate, to defy methodological preachments of the worst kind, the tacit ones.

REFERENCES

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^* From Journal of ‘Economic Methodology 2, no. 1 (June 1995): 1-33.

¹“[M]ethod-talk is asserted to be taboo in economics, when in fact it is surpassed in its ubiquity only by discussion of other people’s salaries” (Mirowski 1992, p. 236).

²Paul Samuelson was avowedly joking, but probably only half-joking, when he reported a negative correlation between the fruitfulness of scientific disciplines and “their propensity to engage in methodological discussion.... [S]oft sciences spend time in talking about method because Satan finds tasks for idle hands to do. Nature does abhor a vacuum, and hot air fills up more space than cold” (1963, in Caldwell 1984, p. 188).

³The methodologist “undertakes to second-guess the scientific community”; he “claims prescience,” “pretends to know how to achieve knowledge before the knowledge to be achieved is in place,” insists on “an artificially narrowed range of argument,” and “lay[s] down legislation for science on the basis of epistemological convictions held with a vehemence inversely proportional to the amount of evidence that they work” (McCloskey 1985, pp. 20, 36, 53, 139).

The particular examples of exhortation and taboo mentioned in the text are more mine than McCloskey’s.

⁴K. Klappholz and J. Agassi deplore “the illusion that there can exist in any science methodological rules the mere adoption of which will hasten its progress” and warn against the “belief that, if only economists adopted this or that methodological rule, the road ahead would at least be cleared (and possibly the traffic would move briskly along it).” They will heed only the general “exhortation to be critical and always ready to subject one’s hypotheses to critical scrutiny.” Additional rules to reinforce this general maxim are “likely to be futile and possibly harmful” (1959, pp. 60, 74).

The physicist P. W. Bridgman liked to say that

there is no scientific method as such, but that the most vital feature of the scientist’s procedure has been merely to do his utmost with his mind, no holds barred. This means in particular that no special privileges are accorded to authority or to tradition, that personal prejudices and predilections are carefully guarded against, that one makes continued check to assure oneself that one is not making mistakes, and that any line of inquiry will be followed that appears at all promising... The so-called scientific method is merely a special case of the method of intelligence, and any apparently unique characteristics are to be explained by the nature of the subject matter rather than ascribed to the nature of the method itself. (Bridgman 1955, p. 544)

I think that the objectives of all scientists have this in common—that they are all trying to get the correct answer to the particular problem in hand... What appears to [the working scientist] as the essence of the situation is that he is not consciously following any prescribed course of action, but feels complete freedom to utilize any method or device whatever which in the particular situation before him seems likely to yield the correct answer. In his attack on his specific problem he suffers no inhibitions of precedent or authority, but is completely free to adopt any course that his ingenuity is capable of suggesting to him. No one standing on the outside can predict what the individual scientist will do or what method he will follow ... there are as many scientific methods as there are individual scientists, (pp. 82-83)

Questioning the assumption of one or a few best methods, Fritz Machlup identifies the harmful

attitude of snubbing, disparaging, excommunicating, and prohibiting the working habits of others and of preaching a methodology that implies that they are inferior in scientific workmanship. [Machlup’s footnote below.]

Good “scientific method” must not proscribe any technique of inquiry deemed useful by an honest and experienced scholar. The aggressiveness and restrictiveness of the various methodological beliefs which social scientists have developed—in subconscious attempts to compensate for their feelings of inferiority vis-a-vis the alleged “true scientist”—are deplorable. Attempts to establish a monopoly for one method, to use moral suasion and public defamation to exclude others, produce harmful restraints of research and analysis, seriously retarding their progress.

[Footnote:] ... I have not said anything against the working habits of others and have not questioned anybody’s scientific workmanship. I have dealt with their claims of exclusive possession of the one and only scientific method. (Machlup 1956/1978, p. 344 in chap. 13)

⁵”It’s easy to be cynical about the motivations of the people who write these papers. You don’t progress as an economics professor by solving the real problems of the real economy, at least not in any direct way. Instead, you progress by convincing your colleagues that you are clever. In an ideal world you would demonstrate your cleverness by developing blindingly original ideas or producing definitive evidence about how the economy actually works. But most of us can’t do that, at least not consistently. So professors look for more surefire approaches. And thus the most popular economic theories among the professors tend to be those that best allow for ingenious elaboration without fundamental innovation—ways to show that you are smart by putting old wine in new bottles, usually with fancier mathematical labels” (Krugman 1994, p. 8).

“[T]he technicality and difficulty of Lucas’s [business-cycle] theory... was, in the world of academic economics, an asset rather than a liability. It is cynical but true to say that in the academic world the theories that are most likely to attract a devoted following are those that best allow a clever but not very original young man to demonstrate his cleverness. This has been true of deconstructionist literary theory; it has equally been true of equilibrium business cycle theory. It turned out that Lucas’s initial theory naturally led to the application of a whole new set of mathematical and statistical techniques. A first set of Lucas disciples made academic reputations developing these techniques; later waves of students invested large amounts of time and effort learning them, and were loath to consider the possibility that the view of the economy to which their specialized training was appropriate might be wrong. Indeed, Lucas himself has in the end seemed more interested in his techniques than in what he does with them” (Krugman 1994, p. 52).

In Krugman’s view, political bias also helped make rational-expectations macroeconomics attractive (1994, pp. 52-53).

Mayer also testifies to tacit methodology at work: “New classicals explain business cycles as mostly due to supply shocks because a demand-side explanation is inconsistent with their chosen Walrasian market clearing paradigm” (1993, p. 116).

Mirowski (1992, pp. 241-247) and McCloskey (1992, p. 266) tell the story of the suppression of an invited conference paper by Lawrence Summers (an eminent economist, certainly, associated with New Keynesianism) because of frankness about methodology similar to that of Krugman and Mayer. Summers had entitled his paper “The Scientific Illusion in Macroeconomics” (published elsewhere in 1991).

⁶Jones and Newman 1992 is a good example. The authors argue that technological progress increases potential output but may reduce current output by making current knowledge obsolete and disrupting current adaptations. They adopt the metaphor of goods concealed in holes in the ground in definite amounts each period. Progress increases the amounts of goods available but reshuffles their locations, making knowledge gained from past searches obsolete. A mathematical formulation of this metaphor, with parameters expressing the probability of technological shocks and their effects on productivity, does illuminate questions of welfare and its distribution and of possible policy tradeoffs.

⁷‘William Poole (1994, pp. 60-62) makes a related point: an optimal policy should abolish any observable relation between money growth and GDP growth. He offers an analogy about trying to determine the relation between a car’s speed and its gasoline consumption by muddling together observations made at moments when the car was going uphill, going downhill, and proceeding on level ground, even though the driver was trying to hold the car’s speed steady throughout.

⁸ Higgs further reminds us that people do not act merely out of self-interest in the narrow sense of homo oeconomkus. Sometimes they act from loyalty to a cherished ideology and for the satisfaction of shared membership in a set of noble, right-minded persons (1987, pp. 42-43).

⁹On “argument from intimidation,” see passages from Ayn Rand’s works reprinted in Binswanger 1986, pp. 32-34.

¹⁰Platt insightfully warns of the researcher who is method-oriented rather than problem-oriented.

[A]nyone who asks the question about scientific effectiveness will also conclude that much of the mathematicizing in physics and chemistry today is irrelevant if not misleading... .

The great value of mathematical formulation is that when an experiment agrees with a calculation to five decimal places, a great many alternative hypotheses are pretty well excluded... . But when the fit is only to two decimal places, or one, it may be a trap for the unwary; it may be no better than any rule-of-thumb extrapolation, and some other kind of qualitative exclusion might be more rigorous for testing the assumptions and more important to scientific understanding than the quantitative fit...

Measurements and equations are supposed to sharpen thinking, but, in my observation, they more often tend to make the thinking noncausal and fuzzy. They tend to become the object of scientific manipulation instead of auxiliary tests of crucial inferences.

Many—perhaps most—of the great issues of science are qualitative, not quantitative, even in physics and chemistry. Equations and measurements are useful when and only when they are related to proof; but proof or disproof comes first and is in fact strongest when it is absolutely convincing without any quantitative measurement. (1964, pp. 351-352)

¹¹“Bart Kosko may be exaggerating but not practicing sheer invention:

Career science, like career politics, depends as much on career maneuvering, posturing, and politics as it depends on research and the pursuit of truth. Few know that when they start the game of science. But they learn it soon enough. (1993, p. 40)

Politics lies behind literature citations and omissions, academic promotions, government appointments, contract and grant awards, conference addresses and conference committee-member choices, editorial-board selection for journals and book series, reviewer selection for technical papers and contract proposals and university accreditation status, and most of all, where the political currents funnel into a laserlike beam, in the peer-review process of technical journal articles, (p. 42)

Bartley’s 1990 book is a sustained expression of doubt about the incentives at work in academe. It explores the intrinsically unfathomable character of knowledge, shows to what a limited extent it can be owned and controlled, and argues that universities are not organized so as readily to advance knowledge (Bartley finds them often working against its growth). Chapters on “The Curious Case of Karl Popper” and on the supposed threat that Popper’s philosophy poses to intellectual fashions provide a case study of the book’s contentions.

Hausman 1992, p. 262, also mentions perverse incentives at work in academic economics.

¹²Not referring to academic economics in particular, Mark C. Henrie (1987, p. 333) notes that an “ability to argue any side of any question demonstrates the importance of technique; but technique alone does not provide the student any insight into which view is true. Quite the opposite, it encourages virtuosity of argumentation for what is false, since to argue falsehood persuasively more fully demonstrates command of technique than to argue for what is true.”

I also suspect some inchoate notion that if falsifiability is a good characteristic of a theory, downright falsity is even better.