Economic theory in retrospect
Chapter 17: A Methodological Postscript
Cambridge University Press, 5th Edition, 1996, xx-yy.
How much does economics explain? What are the grounds on which economic theories have been accepted or rejected? What are the characteristics of endurable economic ideas? What practical use is economic knowledge? These were some of the questions posed in the introduction to this book. Have any or all of them been answered in the course of the text?
Since the days of Adam Smith, economics has consisted of the manipulation of highly abstract assumptions, derived either from introspection or from casual empirical observations, in the production of theories yielding predictions about events in the real world. Even if some of the assumptions involved nonobservable variables, the deductions from these assumptions were ultimately related to the observable world: economists wanted to ‘explain’ economic phenomena as they actually occur. In short, economists have always regarded the core of their subject as ‘science’ in the modern sense of the word: the goal was to produce accurate and interesting predictions that were, in principle at least, capable of being empirically falsified. In practice, they frequently lost sight of this scientific objective and the history of economics is certainly replete with tautological definitions and theories so formulated as to defy all efforts at falsification. But no economist writing on methodology, whether in the nineteenth or in the twentieth century, has ever denied the relevance of the now widely accepted demarcation rule of Popper: theories are ‘scientific’ if they are falsifiable, at least in principle, and not otherwise. Such methodologists as Senior, J. S. Mill, Cairnes, Sidgwick, Jevons, Marshall, John Neville Keynes, Böhm-Bawerk and Pareto frequently emphasised other matters and undoubtedly underemphasised the problem of devising appropriate empirical tests of theories but nothing they wrote denied
the idea that to ‘explain’ is ultimately to predict that such and such will or will not happen.
Robbins’s Essay on the Nature and Significance of Economic Science (1932) is frequently cited as a prime example of the opposite tendency, emphasising the irrelevance of empirical testing to the truth of economic theories. But the purpose of Robbins’s book was to purge economics of value judgements. It is not clear whether Robbins really wanted economists to abandon welfare economics altogether or merely to separate ‘positive’ from ‘normative’ economics, so as to deny scientific status to the latter. Nor is it clear, even after repeated reading, whether he really meant to commit himself to ‘radical apriorism’, despite the fact that many passages in the book do invite that interpretation. ‘Radical apriorism’ holds that economic theories are simply a system of logical deductions from a series of postulates derived from introspection, which are not themselves subject to empirical verification. In stark contrast to radical apriorism is ‘ultra-empiricism’, which refuses to admit any postulates or assumptions that cannot be independently verified; ultra-empiricism, in other words, asks us to begin with facts, not assumptions. But an ‘apriorist’ may agree that the predicted results deduced from subjective assumptions, if not the subjective assumptions themselves, should be subject to empirical testing. And few ‘ultra-empiricists’, no matter how much they insist that all scientifically meaningful statements must be falsifiable by observation, go so far as to deny any role whatever to tautologies and identities in scientific work. The controversy is over matters of emphasis and most economists ever since Senior and J. S. Mill, the first methodologists of the subject, have occupied the middle ground between ‘radical apriorism’ and ‘ultra-empiricism’.
Nevertheless, the striking fact about the history of economics is how often economists have violated both their own and later methodological prescriptions. The classical economists emphasised the fact that the conclusions of economics rest ultimately on postulates derived as much from the observable ‘laws of production’ as from subjective introspection. Methodological disputes in the classical period took the form of disagreement over the realism and relevance of the underlying assumptions on which the whole deductive structure was built, while everyone paid lip service to the need to check the predictions of logical deductions against experience. The empirical verification of economics was regarded as too simple to require argument: it was simply a matter of ‘look and see’. But despite J. S. Mill’s authoritative pronouncement that ‘we cannot too carefully endeavour to verify our theory, by comparing... the results which it would have led us to predict, with the most trustworthy accounts we can obtain of those which have actually been realised’, no real effort was made to test classical doctrines against the body of statistical material that had been accumulated by the middle of the nineteenth century. The debatable issues in Ricardian economics all hinged on the relative weight of forces making for historically diminishing and increasing returns in the production of wage goods. This question was capable of being resolved along
empirical lines, given the fact that some information on money wages and the composition of working class budgets had been made available by the 1840s and that the concept of a price index had passed by this time into general currency. Yet despite the knowledge that population was no longer ‘pressing’ upon the food supply, that ‘agricultural improvements’ were winning the race against numbers, that the rise of productivity in agriculture was steadily reducing the real cost of producing wage goods, the classical writers clung to a belief in the imminent danger of natural resource scarcities.
The standard defence was to attribute every contradiction to the strength of ‘counteracting tendencies’. In effect, the classical economists treated certain variables that entered into their analysis as exogenously determined, such as the rate of technical improvement in agriculture, the disposition of the working class to practise family limitation, and the supply of entrepreneurship. Instead of confessing their ignorance about the exogenous variables, however, they advanced bold generalisations about their probable variations through time. For the most part, they did not raise the question whether the exogenous variables were really independently determined constants. In addition, they failed to inquire whether the phenomena labelled ‘counteracting tendencies’ entered, as it were, as additional parameters to the original equations of their model, or whether they in fact altered the structure of the equations themselves. It was because the motives for family limitation were not in fact independent of the outcome of the race between population and the food supply that the Maithusian theory of population predicted so poorly. It was because Ricardian economics failed to deal with the problems of technical change in agriculture - falling back upon the belief, denied by historical experience, that English landlords were not ‘improvers’ - that the Corn Laws did not entail the harmful effects that Ricardo had predicted. Had the classical economists acted on Mill’s urging to ‘carefully endeavour to verify our theory’ such weaknesses in the structure would have come to light and led to analytical improvements. As it was, the absence of any alternative theory to that of Ricardo, having equal scope and practical significance, discouraged revisions and promoted a defensive methodological attitude.
Marx is another case in point. His tendency to attribute all discrepancies between his theory and the facts to the dialectical ‘inner contradictions’ of capitalism provided him with a perfect safety valve against refutations. In addition, he was a past master of the ‘apocalyptic fallacy’ (see chapter 3, section 4): there were ‘laws of motion’ which were confirmed by evidence, unless of course ‘counteracting tendencies’ were at work, in which case the evidence would soon bear out the law in question. Nevertheless, the ambiguity with which Marx formulated his secular predictions suggests that he was well aware that there is some weight of contrary evidence sufficient to refute any so-called ‘law’ - ‘laws of motion’ that are never verified do not deserve the label. Thus, even Marx subscribed in the final analysis to the methodological canon that economic theories should be capable of being falsified; it was simply that he could not bring himself to face up to the requirements of this canon.
The model of perfect competition that evolved in the heyday of the Marginal Revolution owed much to the older welfare propositions of the loosely stated Invisible Hand type. By limiting the scope of the analysis, however, greater rigour in model construction became possible. The argument was typically related to a few continuous variables and it was confined to explaining the direction of small changes in these variables. All the growth-producing factors, such as the expansion of wants, population growth, technical change and even the passage of time itself, were placed in the box of ceteris paribus. The remaining system of endogeneous variables was then shown to have a unique steady-state solution. The problem of achieving equilibrium in the first place was passed over by the method of comparative statics: analysis usually began with an equilibrium situation and then traced out the adjustment process to a new stable equilibrium given a change in the value of one or more of the parameters. Walras saw the problem and deceived himself in thinking that he had solved it: his concept of tâtonnement, or Edgeworth’s analogous notion of recontracting, demonstrated in effect that markets would attain equilibrium by one bold leap from any initial starting point, thus effectively ruling out the disturbances created by disequilibrium trading. Indeterminacy of equilibrium was eliminated by excluding all interdependence among utility and production functions, and stability of equilibrium was ensured by placing various restrictions on the underlying functions and by abstracting from ignorance and uncertainty. The entire procedure was justified by the short-run purpose of the analysis, although this did not prevent excursions into welfare economics involving long-run considerations.
The endogenous variables manipulated in neo-classical models were frequently incapable of being observed, even in principle, and most of the theorems that emerged from the analysis likewise failed to be empirically meaningful. Furthermore, the microeconomic character of the analysis made testing difficult in view of the fact that most available statistical data referred to aggregates: the problem of deducing macroeconomic theorems from microeconomic propositions was not faced squarely until Keynes’s work revealed that there was a problem. In addition, the rules for legitimately treating certain variables as exogenous - they must be independent of the endogenous variables in the model, or related to them in a unidirectional manner, and they must be independent of each other - were constantly violated. It is obvious that tastes, population and technology not only affect and are affected by the typical endogeneous variables of neo-classical models but that they affect each other in turn.
The standard excuse for treating as exogenous variables that clearly are not exogenous is analytical tractability and expository convenience. For a whole range of practical problems, it is in fact a very good excuse. But the temptation to read more significance into the analysis than is inherent in the procedure is irresistible and most neo-classical writers succumbed to it. Ambitious propositions about the desirability of perfect competition were laid down with insufficient scruples. Of course, it was recognised that competition was a regulatory device of limited applicability.
Important differences between private and social costs, the phenomenon of ‘natural monopoly’ via increasing returns to scale and ethically undesirable distributions of income, not to mention the existence of ‘public goods’ and second-best problems, gave scope to government action. But these qualifications were grafted on, rather than incorporated in, the competitive model. Furthermore, the growth-producing factors that were now regarded as noneconomic in character ceased to receive systematic analysis. Having marked the boundaries of economics, neo-classical writers openly confessed noncompetence outside that boundary and were satisfied to throw out a few commonsense conclusions and occasionally a suggestive insight. It takes no effort of historical perspective to realise that the second half of the nineteenth century invited a complacent attitude to economic growth: it is only natural that an author like Marshall should think that growth would take care of itself, provided that ‘free’ competition supported by minimum state controls would furnish an appropriate sociopolitical environment. Nevertheless, the result was to leave economics without a theory of growth or development other than the discouraging one that the long-period evolution of an economy depends largely on the neglected noneconomic factors.
The besetting methodological vice of neo-classical economics was the illegitimate use of microstatic theorems, derived from ‘timeless’ models that excluded technical change and the growth of resources, to predict the historical sequence of events in the real world. A leading example of this vice was the explanation of the alleged constancy of the relative shares of labour and capital by the claim that the aggregate production function of the economy is of the Cobb-Douglas type, although the theory in question referred to microeconomic production functions and no reasons were given for believing that Cobb-Douglas microfunctions could be neatly aggregated to form a Cobb-Douglas macrofunction. But we have witnessed numerous other instances of the vice: the argument that welfare can be improved by taxing increasing-cost industries and subsidising decreasing-cost industries (see chapter 9, section 16; chapter 10, section 6); the theory that conditions of monopolistic competition lead to excess capacity (see chapter 10, section 9); the idea that existence of an equilibrium solution ensures stability of equilibrium (see chapter 10, section 21); the view that factor payments in accordance with marginal productivity provide a clear rule for increasing aggregate employment in the economy and a theory of the determination of relative shares (see chapter 11, section 9); the notion that the failure of concentration ratios to rise in all industries shows that there is an optimum size of firms (see chapter 11, section 17); the proposition that the capital intensity or ‘average period of production’ of an economy is a monotonic function of the rate of interest (see chapter 12, section 1 5), that capital intensity falls at the upper turning point and rises at the lower turning point of the business cycle because of the Ricardo Effect (see chapter 12, section 27) and that revaluation of the capital stock as a change in investment alters the rate of interest is the key to the theory of capital accumulation (see chapter 12, section 41); the theory that the economy tends continually to return to a given natural rate of unemployment because deviations from it are due to the failure of expectations to catch up with events, which failure
can only be momentary (see chapter 16, section 24); and, lastly - the vice writ large - the view that perfect competition is a sufficient condition for allocative efficiency (see chapter 13, section 13).
Since economic activity takes place in time, can any ‘timeless’ economic theory ever hope to predict anything? We must begin by disenchanting ourselves of the idea that economic predictions must be quantitative in character to qualify as scientific predictions. Clearly, the predictions of most economic models are qualitative rather than quantitative in nature: they specify the directions of change of the endogenous variables in consequence of a change in the value of one or more exogenous variables, without pretending to predict the numerical magnitude of the change. In other words, all neo-classical economics is about the signs of first- and second-order partial derivatives and that is virtually all it is about.
As Samuelson put it in the Foundations of Economic Analysis: ‘The method of comparative statics consists of the study of the response of our equilibrium unknowns to designated changes in the parameters... In the absence of complete quantitative information concerning our equilibrium equations, it is hoped to be able to formulate qualitative restrictions on slopes, curvatures, etc., of our equilibrium equations so as to be able to derive definite qualitative restrictions upon the responses of our system to changes in certain parameters.’ This is what he called the ‘qualitative ca1cu1us’, that is, the attempt to predict directions of change without specifying the magnitude of the change. Now it is an obvious fact that the mere presence of an equilibrium solution for a comparative static model does not guarantee that we can apply the ‘qualitative calculus’: all the marginal equalities in the world may not add up to a testable prediction. This is perfectly familiar from the theory of household behaviour: whenever substitution and income effects work in opposite directions, the outcome depends on relative magnitudes and hence on more than the first- and second-order conditions for a maximum. A moment’s reflection, therefore, will show that a great many neo-classical theories are empty from the viewpoint of the ‘qualitative calculus’; unless they are fed with more facts to further restrict the relevant functions, they tell us only that equilibrium is what equilibrium must be. If that is so, why have economists not abandoned all such empty models?
In 1953, Friedman published an essay on ‘The Methodo1ogy of Positive Economics’ which quickly generated a methodological controversy almost as heated as that produced by Robbins’s Essay in 1932. Friedman argued that most traditional criticism of economic theory had scrutinised assumptions instead of testing implications; the validity of economic theory, he contended, is to be established, not by the descriptive ‘realism’ of its premises, but by the accuracy of the predictions with which it is concerned. Friedman’s methodological position would seem to be unassailable - most assumptions in economic theory involve unobservable variables and it is meaningless to demand that such variables should conform to ‘reality’ - until it is realised that he is insisting on predictive accuracy as the sole criterion of validity.
If a theory is rigorously formulated to the extent of being axiomatised, realism of
assumptions is logically equivalent to realism of implications. The trouble is that few economic theories have been successfully axiomatised and, in general, economic hypotheses are not tightly linked to their assumptions in an absolutely explicit deductive chain. In that sense, evidence from direct observation of such behavioural assumptions as transitive preference orderings among consumers, or such technical assumptions as the constant-returns-to-scale characteristics of the production function, is capable of shedding additional light on a theory. But precisely because the theory is loosely formulated, such evidence can never do more than suggest that the theory is worth testing in terms of its falsifiable consequences. In short, Friedman is quite right to attack the view that realism of assumption is a test of the validity of a theory different from, or additional to, the test of predictive accuracy of implications.
At the same time, it must be admitted that the edict: ‘test implications, instead of assumptions’, is not very helpful by itself. The criterion of falsifiable implications can be interpreted with different degrees of stringency. If the predictions of a theory are not contradicted by events, the theory is accepted with a degree of confidence that varies uniquely with the magnitude of the supporting evidence. But, what if it is contradicted? If no alternative ‘simple’, ‘elegant’ and ‘fruitful’ theory explaining the same events is available - for these are the grounds on which we choose between theories predicting the same consequences - frequent contradiction will be demanded. But what degree of frequency of contradictions will prove persuasive? Economists abhor a theoretical vacuum as much as nature abhors a physical one and in economics, as in the other sciences, theories are overthrown by better theories, not simply by contradictory facts. Since there are few opportunities to conduct controlled experiments in the social sciences, so that contradictions are never absolute, economists are bound to be more demanding of falsifying evidence than, say, physicists. By the standards of accuracy applied to predictions in the natural sciences, economics make a poor showing and hence economists are frequently forced to resort to indirect methods of testing hypotheses, such as examining the ‘realism’ of assumptions or testing the implications of theories for phenomena other than those regarded as directly relevant to a particular hypotheses. This opens the door to the easy criticism that economics is a failure because most of its typical assumptions - such as transitive preferences, profit maximisation at equal risk levels, independence of utility and production functions, and the like - do not conform to behaviour observed in the real world. If economics could conclusively test the implications of its theorems, no more would be heard about the lack of realism of its assumptions. But conclusive once-and-for-all testing or strict refutability of theorems is out of the question in economics because all its predictions are probabalistic ones.
Once we have accepted the basic idea that the presence of ‘disturbing’ influences surrounding economic events precludes absolute falsifiability of economic theorems, it is easy to see why economics contains so many nonfalsifiable concepts. Many economic phenomena have not yet lent themselves to systematic theorising and yet economists do not wish to remain silent because of some methodological
fiat that real science should consist only of falsifiable theorems. A ‘theory’ is not to be condemned merely because it is as yet untestable, not even if it is so framed as to preclude testing, provided it draws attention to a significant problem and provides a framework for its discussion from which a testable implication may someday emerge. It cannot be denied that many so-called ‘theories’ in economics have no empirical content and serve merely as filing systems for classifying information. To demand the removal of all such heuristic devices and theories in the desire to press the principle of falsifiability to the limit is to proscribe further research in many branches of economies. It is perfectly true that economists have often deceived themselves - and their readers - by engaging in what Leontief once called ‘implicit theorising’: presenting tautologies in the guise of substantive contributions to economic knowledge. But the remedy for this practice is clarification of purpose, not radical and possibly premature surgery.
Furthermore, it is not always easy to draw the line between tautologies and falsifiable propositions. A theory that is obstensibly a mere collection of deductions from ‘convenient’ assumptions, so framed as to be nonfalsifiable under any conceivable circumstance, may be reinterpretable as a verifiable proposition. After a hundred years of discussion, economists are still not quite agreed as to whether the Malthusian theory of population is nothing but a very complicated tautology that can ‘explain’ any and all demographic events, or a falsifiable prediction about per capita income in the event of population growth. Whatever Malthus’s own intention, the theory can be so restated as to meet the criterion of falsifiability, in which case it has in fact been falsified. The concept of a negatively inclined demand curve in conjunction with an inclusive ceteris paribus clause is not a falsifiable concept, because if quantity and price are both observed to decline together in the absence of changes in other prices, incomes and expectations, it is always possible to save the original proposition by the contention that tastes have changed. But the concept can be rendered falsifiable if we hypothesise that tastes are stable over the relevant period of time, or that tastes change in a predictable fashion over time. The assumption of stable tastes is a genuine empirical hypothesis and all work on statistical demand curves has been concerned in one way or another with testing this hypothesis.
The same comments apply to the supply side. The notion of a production function - the spectrum of all known techniques of production - is by itself a concept so general as to be empty. Businessmen have not experienced all known techniques and the cost of obtaining more experience with techniques is not negligible; the vital difference for an individual firm is not between known and unknown but between tried and untried methods of production. The convention of putting all available technical knowledge in one box called ‘production functions’ and all advances in knowledge in another box called ‘innovations’ has no simple counterpart in the real world where most innovations are ‘embodied’ in new capital goods, so that firms move down production functions and shift them at one and the same time. Nevertheless, the concept of a production function can be given an empirical interpretation if we hypothesise that production functions are stable. This may well be
very difficult to verify in practice but in principle it is verifiable and work in recent years on ‘embodied’ and ‘disembodied’ capital-growth models, however inconclusive it has proved to be, has been precisely concerned with testing the hypothesis of stable production functions. And so the two fundamental propositions of neo-classical price theory, to wit, positive excess demand leads to a rise in price and an excess of price over cost leads to a rise in output, are both capable of being falsified, despite the fact that they have frequently been laid down as immutable laws of nature.
To drive the point home, let the reader question whether the following familiar propositions - the list is merely suggestive - constitute falsifiable or heuristic statements; if the former, whether they are falsifiable in principle or in practice and, if the latter, whether and in what sense they are defensible as fruitful points of departure for further analysis.
1 A specific tax on an article will raise its price by less than the tax if the elasticity of demand is greater than zero and the elasticity of supply is less than infinity.
2 The elasticity of demand for a commodity is governed by the degree of substitutability of that commodity in consumption.
3 The impact effect of a rise in money wages in a competitive industry is to reduce employment.
4 In the absence of technical change, a rise in the average capital-labour ratio of an economy causes wage rates to rise and capital rentals to fall.
5 A laboursaving innovation is one that reduces capital’s relative share of output at given factor prices.
6 An ‘industry’ is a group of firms whose products are perfect or near-perfect substitutes for each other.
7 Perfect competition is incompatible with increasing returns to scale.
8 Profit maximisation is a plausible assumption about business behaviour because the competitive race ensures that only profit maximisers survive.
9 An equal rise in government expenditures and receipts will raise national income by the amount of that rise if the community’s marginal propensity to consume is positive and less than one.
10 A tax imposed on an industry whose production function is linearly homogeneous results in a loss of consumers’ surplus greater than the amount of the tax receipts.
11 Increasing or diminishing returns to scale are always due to the indivisibility of some input.
12 Price expectations are always ‘rational’ in the sense that the expected mean value of the probability distribution of forecasted prices is identical to the mean value of the probability distribution of actual prices.
An hour spent thinking about these propositions will convince anyone that it is not easy to make up one’s mind whether particular economic theories are falsifiable or not; it is even more difficult to know what to make of these theories that are not falsifiable; and as for the ones that are indeed falsifiable, it is still more difficult to
think of appropriate methods of putting them to the test. In short, empirical testing may be the heart of economics but it is only the heart. 
Even if all economics could be neatly divided into testable and untestable theories and even if unanimous agreement had been obtained on the validity of the testable theories, we would still have to assess their significance or relevance. This introduces the problem of normative as distinct from positive economics. After a series of attacks on utilitarian welfare economics, a new Paretian welfare economics was erected in the 1930s that purported to avoid interpersonal comparisons of utility. ‘Scientific’ welfare economics has lately come in for its share of destructive criticism and some economists have echoed once again the old Seniorian cry that economics should be wholly ‘positive’ in character. But whatever we may think of modern welfare economics, there can be no doubt that the desire to evaluate the performance of economic systems has been the great driving force behind the development of economic thought and the source of inspiration of almost every great economist in the history of economics.
Indeed, it would be difficult to imagine what economics would be like if we succeeded in eliminating all vestiges of welfare economics. For one thing, we would never be able to discuss efficient allocation of resources, for the question of efficient allocation of scarce means among competing ends cannot even be raised without a standard of evaluation. The fact that the price system is a particular standard of evaluation, namely, one that counts every dollar the same no matter whose dollar it is, should not blind us to the fact that acceptance of the results of competitive price systems is a value judgement. The price system is an election in which some voters are allowed to vote many times and the only way people can vote is by spending money. Economists are constantly engaged in making the fundamental value judgement that only certain types of individual preferences are to count and, furthermore, to count equally. We all know, of course, why economics has confined its attention to those motives for action that can be evaluated with ‘the measuring rod of money’
 A few words about a subject like psychoanalysis will show that the difficulties of applying the falsifiability criterion are not confined to economics. Is psychoanalysis a science or merely a psychic poultice for the rejects of industrial civilisation? If it is a science, are its leading concepts – the Oedipus Complex; the division of the mind into id, ego and superego; sublimation; repression; transference; and the like - falsifiable? Despite the fact that psychoanalysis is now almost a century old, there is still very little agreement on these questions either among analysts or among critics of psychoanalysis. In one sense, the situation in psychoanalysis is much worse than economics. At least economists do agree that economics is a science and that its principles must ultimately stand up to scientific testing. Psychoanalysts, however, sometimes argue that what Freud tried to do was not to explain neurotic symptoms in terms of cause and effect but simply to make sense of them as disguised but meaningful communication; psychoanalysis is, therefore, an art of healing and must be judged in terms of its success in curing patients. Even so, there has been surprisingly little research on psychoanalytic ‘cures’, and, of course, it is difficult to see how psychoanalysis could cure patients if its interpretations of neurotic behaviour did not somehow correspond with reality. At any rate, it would be fair to say that the status of the falsifiability criterion in economics is about halfway between its status in psychoanalysis and its status in nuclear physics.
but the fact remains that value judgements are involved at the very foundation of the science.
If economists are necessarily committed to certain value judgements at the outset of analysis, how can it be claimed that economics is a science? This innocent question has been productive of more methodological mischief than any other posed in this chapter. Ever since Max Weber attempted to settle this question by defining the prerequisites of ethical neutrality in social science, there has been an endless debate on the role of value judgements in subjects like sociology, political science and economics. Critics of economics have always been convinced that the very notion of objective economics divorced from value judgements is a vain pretence. Working economists, on the other hand, more or less aware of their own value judgements, and very much aware of the concealed value judgements of other economists with whom they disagree, never doubted that the distinction between positive and normative economics was as clear-cut as the distinction between the indicative and imperative mood in grammar. But how can there be such total disagreement on what appears to be a perfectly straightforward question?
The orthodox Weberian position on wertfrei social science is essentially a matter of logic: as David Hume taught us, ‘you can’t deduce ought from is’. Thus, the descriptive statements or behavioural hypotheses of economics cannot logically entail ethical implications. It is for this reason that J.N. Keynes, the leading neo-classical methodologist, could write as long ago as 1891: ‘the proposition that it is possible to study economic uniformities without passing ethical judgements or formulating economic precepts seems in fact so little to need proof, when the point at issue is clearly grasped, that it is difficult to say anything in support of it that shall go beyond mere truism’. Nevertheless, time and time again it has been claimed that economics is necessarily value-loaded and that, in Myrdal’s words, ‘a “disinterested social science” has never existed and, for logical reasons, cannot exist’. When we sort out the various meanings that such assertions carry, they reduce to one or more of the following propositions: (1) the selection of questions to be investigated by economics may be ideologically biased: (2) the answers that are accepted as true answers to these questions may be likewise biased, particularly since economics abounds in contradictory theories that have not yet been tested; (3) even purely factual statements may have emotive connotations and hence may be used to persuade as well as to describe; (4) economic advice to political authorities may be value-loaded because means and ends cannot be neatly separated and hence policy ends cannot be taken as given at the outset of the exercise; and (5) since all practical economic advice involves interpersonal comparisons of utility and these are not testable, practical welfare economics almost certainly involves value judgements. Oddly enough, all of these assertions are perfectly true but they do not affect the orthodox doctrine of value-free social science in any way whatsoever.
Proposition (1) simply confuses the origins of theories with the question of how they may be validated. Schumpeter’s History of Economic Analysis continually reminds the reader that all scientific theorising begins with a ‘Vision’ - ‘the pre-analytic cognitive act that supplies the raw material for the analytic effort’ - and in
this sense science is ideological at the outset. But that is quite a different argument from the one that contends that for this reason the acceptance or rejection of scientific theory is also ideological. Similarly, both propositions (1) and (2) confuse methodological judgements with normative judgements. Methodological judgements involve criteria for judging the validity of a theory, such as levels of statistical significance, selection of data, assessment of their reliability and adherence to the canons of formal logic, all of which are indispensable in scientific work. Normative judgements, on the other hand, refer to ethical views about the desirability of certain kinds of behaviour and certain social outcomes. It is the latter which alone are said to be capable of being eliminated in positive science. As for propositions (3) and (4), it may be granted that economists have not always avoided the use of honorific definitions and persuasive classifications. Nor have they consistently refused to recommend policy measures without first eliciting the policy maker’s preference function. But these are abuses of the doctrine of value-free economics and do not suffice to demonstrate that economics is necessarily value-loaded. We conclude that when economists make policy recommendations, they should distinguish as strongly as possible between the positive and the normative bases for their recommendations. They should also make it clear whether their proposals represent second-best compromises or concessions to considerations of political feasibility. But they should not refuse to advise simply because they do not share the policy maker’s preference function and they should stoutly resist the argument that economic advice depends entirely on the particular economist that is hired.
Proposition (5) deserves separate comment. Welfare economics, whether pure or applied, obviously involves value judgements, and, as we noted earlier, the idea of value-free welfare economics is simply a contradiction in terms. This question would never have arisen in the first place if the new Paretian welfare economics had not adopted the extraordinary argument that a consensus on certain value judgements renders these judgements ‘objective’; apparently, the only value judgements that fail to meet this test involve interpersonal comparisons of utility and these were therefore banned from the discussion.
Despite obeisance to the concept of ‘positive’ economics and the principle of verifying predictions by submitting them to evidence, most economists who have had qualms about the value of received doctrine have stilled these qualms, not by searching for tangible evidence of the predictive power of economic theory, but by reading the substantive contributions of leading critics of orthodox analysis. Bad theory is still better than no theory at all and, for the most part, critics of orthodoxy had no alternative construction to offer. One obvious exception to this statement are Marxist critics. Another possible exception are the American Institutionalists. Indeed, no discussion of methodology in economics is complete without a mention of this greatest of all efforts to persuade economists to base their theories, not on analogies from mechanics, but on analogies from biology and jurisprudence.
‘Institutional economics’, as the term is narrowly understood, refers to a move-
ment in American economic thought associated with such names as Veblen, Mitchell and Commons. It is no easy matter to characterise this movement and, at first glance, the three central figures of the school seem to have little in common: Veblen applied an inimitable brand of interpretative sociology to the working creed of businessmen; Mitchell devoted his life to the amassing of statistical data, almost as an end in itself and Commons analysed the workings of the economic system from the standpoint of its legal foundations. More than one commentator has denied that there ever was such a thing as ‘institutional economics’, differentiated from other kinds of economics. But this is tantamount to asserting that a whole generation of writers in the interwar years deceived themselves in thinking that they were rallying around a single banner. Surely, they must have united over certain principles?
If we attempt to delineate the core of ‘institutionalism’, we come upon three main features, all of which are methodological: (1) dissatisfaction with the high level of abstraction of neo-classical economics and particularly with the static flavour of orthodox price theory; (2) a demand for the integration of economics with other social sciences, or what might be described as faith in the advantages of the interdisciplinary approach; and (3) discontent with the casual empiricism of classical and neo-classical economics, expressed in the proposal to pursue detailed quantitative investigations. In addition, there is the plea for more ‘social control of business’, to quote the title of J. M. Clark’s book, published in 1926; in other words, a favourable attitude to state intervention. None of the four features is found in equal measure in the works of the leading institutionalists. Veblen cared little for digging out the facts of economic life and was not fundamentally opposed to the abstract deductive method of neo-classical economics. Moreover, he refused to admit that the work of the German Historical School constituted scientific economics. What he disliked about orthodox economics was not its method of reaching conclusions, but its underlying hedonistic and atomistic conception of human nature - in short, the Jevons-Marshall theory of consumer behaviour. Moreover, he dissented vigorously from the central implication of neo-classical welfare economics that a perfectly competitive economy tends, under certain restricted conditions, to optimum results. This amounted to teleology, he argued, and came close to an apology for the status quo. Economics ought to be an evolutionary science, Veblen contended, meaning an inquiry into the genesis and growth of economic institutions; the economic system should be viewed, not as a ‘self-balancing mechanism’, but as a ‘cumulatively unfolding process’. He defined economic institutions as a complex of habits of thought and conventional behaviour; it would seem to follow, therefore, that ‘institutional economics’ comprised a study of the social mores and customs that becomes crystallised into institutions. But what Veblen actually gives the reader is Kulturkritik, dressed up with instinct psychology, racist anthropology and a flight of telling adjectives: ‘conspicuous consumption’, ‘pecuniary emulation’, ‘ostentatious display’, ‘absentee ownership’, ‘discretionary control’ - these are just a few of Veblen’s terms that have passed into the English language. It was a mixture so unique and individual to Veblen that even his most avid disciples were unable to
extend or develop it. Books like The Theory of the Leisure Class (1899) and The Theory of Business Enterprise (1940) appear to be about economic theory but they are actually interpretations of the values and mores of the ‘captains of industry’.
To fully appreciate the difficulty of evaluating Veblen’s ideas, let us take one striking example. No matter what book of Veblen we open, we find the idea that life in a modern industrial community is the result of a polar conflict between ‘pecuniary employments’ and ‘industrial emp1oyments’, or ‘business enterprise’ and ‘the machine process’, or ‘vendibility’ and ‘serviceability’, that is, making money and making goods. There is a class struggle under capitalism, not between capitalists and proletarians, but between businessmen and engineers. Pecuniary habits of thought unite bankers, brokers, lawyers and managers in a defence of private acquisition as the central principle of business enterprise. In contrast, the discipline of the machine falls on the workmen in industry and more especially on the technicians and engineers that supervise them. It is in these terms that Veblen describes modern industrial civilisation. As we read him, we have the feeling that something is being ‘explained’. Yet what are we really to make of it all? Is it a contrast between subjective and objective criteria of economic welfare? Is it a plea to abandon the emphasis on material wealth, implying in the manner of Galbraith that we would be better off with more public goods and less trivia? Is it a demonstration of a fundamental flaw in the price system? Is it a call for a technocratic revolution? There is evidence in Veblen’s writings for each of these interpretations but there is also much evidence against all of them. Furthermore, Veblen never tells us how to find out whether his polarities explain anything at all. It is not simply that he never raised the question of how his explanations might be validated but that he is continually hinting that a description is a theory, or, worse, that the more penetrating is the description, the better is the theory.
Mitchell, on the other hand, was a thinker of a different breed. He showed little inclination for methodological attacks on the preconceptions of orthodox economics and eschewed the interdisciplinary approach. His ‘institutionalism’ took the form of collecting statistical data on the notion that these would eventually furnish explanatory hypotheses. He was the founder of the National Bureau of Economic Research and the chief spokesman of the concept that has been uncharitably described as ‘measurement without theory’.
Commons alone wrote a book specifically entitled Institutional Economics (1934) which, together with his Legal Foundations of Capitalism (1926), analysed the ‘working rules’ of ‘going concerns’ that governed ‘individual transactions’; ‘transactions’, ‘working rules’, ‘the going concern’, these were the building blocks of his system. In his own day, Commons was much better known as a student of labour legislation. His theoretical writings are as suggestive as they are obscure and few commentators have succeeded in adequately summarising them.
Thus, despite certain common tendencies, the school of ‘institutional economics’ was never more than a tenuous inclination to dissent from orthodox economics. This may explain why the phrase itself has degenerated into a synonym for ‘descriptive economics’, a sense in which it may be truly said: ‘we are all institutional economists
now’. Of course, if we are willing to recast our terms and to include in our net all those that have contributed to ‘economic sociology’ - which Schumpeter regarded as one of the four fundamental fields of economics, the other three being economic theory, economic history and statistics - we would have to treat Marx, Schmoller, Sombart, Max Weber, Pareto and the Webbs, to cite only a few, as ‘institutional economists’. It has been said that if economic analysis deals with the question of how people behave at any time, ‘economic sociology’ deals with the question of how they come to behave as they do. Economic sociology, therefore, deals with the social institutions that are relevant to economic behaviour, such as governments, banks, land tenure, inheritance law, contracts and so on. Interpreted in this way, there is nothing to quarrel with. But this is hardly what Veblen, Mitchell and Commons thought they were doing. Institutional economics was not meant to complement economic analysis as it had always been understood but to replace it.
There are few economists today who would consider themselves disciples of Veblen, Mitchell and Commons; although there is an Association of Evolutionary Economics, publishing its own journal, the Journal of Economic Issues, which is determined to revitalise the spirit of the founding fathers of American institutionalism. Nevertheless, the institutionalist movement ended for all practical purposes in the 1930s. This is not to deny that there were lasting influences. Mitchell’s contribution to our understanding of the business cycle and in particular to the revolution in economic information that separates twentieth- from nineteenth-century economics is too obvious to call for comment. There is a renewed interest in evolutionary economics and “the new institutional economics” (property rights, transaction costs, etc.), which holds out great promise. But the old, institutionalist economics of Veblens and Commons never did supply a viable alternative to neo-classical economics and for that reason, despite the cogency of much of the criticisms of orthodoxy, it gradually faded away. The moral of the story is simply this: it takes a new theory, and not just the destructive exposure of assumptions or the collection of new facts, to beat an old theory.
There are no simple rules for distinguishing between valid and invalid, relevant and irrelevant theories in economics. The criterion of falsifiability can separate propositions into positive and normative categories and thus tell us where to concentrate our empirical work. Even normative propositions can often be shown to have positive underpinnings, holding out the prospect of eventual agreement on the basis of empirical evidence. Nevertheless, a core of normative theorems always remains for which empirical testing is irrelevant and immaterial. Moreover, there is an undetermined body of economic propositions and theorems which appear to be about economic behaviour but which do not result in any predictable implications about that behaviour. In short, a good deal of received doctrine is metaphysics. There is nothing wrong with this, provided it is not mistaken for science. Alas, the history of economics reveals that economists are as prone as anyone else to mistake chaff for wheat and to claim possession of the truth when all they possess are intricate series
of definitions or value judgements disguised as scientific rules. There is no way of becoming fully aware of this tendency except by studying the history of economics. To be sure, modern economics provides an abundance of empty theories parading as scientific predictions or policy recommendations carrying concealed value premises. Nevertheless, the methodological traps are so subtle and insidious that the proving ground cannot be too large. One justification for the study of the history of economics, but of course only one, is that it provides a more extensive ‘laboratory’ in which to acquire methodological humility about the actual accomplishments of economics. Furthermore, it is a laboratory that every economist carries with him, whether he is aware of it or not. When someone claims to explain the determination of wages without bringing in marginal productivity, or to measure capital in its own physical units, or to demonstrate the benefits of the Invisible Hand by purely objective criteria, the average economist reacts almost instinctively but it is an instinct acquired by the lingering echoes of the history of the subject. Why bother then with the history of economic theory? Because it is better to know one’s intellectual heritage than merely to suspect it is deposited somewhere in an unknown place and in a foreign tongue. As T.S. Eliot put it: ‘Someone said: “The dead writers are more remote from us because we know so much more than they did.” Precisely, and they are that which we know.’