Brian J. Loasby
Hypothesis and Paradigm in the Theory of the Firm 
Economic Journal, 81 (324)
Dec., 1971, 863-885.
THOUGH here applied to a particular subject area, the arguments presented in this article have a much wider significance. The article begins with an emphasis on the kinds of abstraction which are necessary in a study of complex systems, and an exposition, in the context of economics, of the ideas developed by T. S. Kuhn to analyse theoretical innovation in the physical sciences.  This apparatus is then used to illuminate some critical developments in the theory of value, leading up to an examination of the credentials of behavioural theories of the firm. In the process, it reveals some widespread misconceptions among economists about the nature of economic science, and shows how these misconceptions have not only been responsible for much confusion but have also critically influenced the development of economic theory.
Logically, as well as historically, the development of economics as an important and distinctive discipline derives from the increasing extent and complexity of the division of labour. It is true that an allocation problem exists whenever an individual’s resources are not sufficient for the satisfaction of all his wants; but although the economic problems of Robinson Crusoe are very convenient for elucidating some features of the elementary analysis of choice, they are scarcely adequate material for a major field of study. That material is to be found in the interdependent choices which result from an elaborate division of labour - between individuals, between firms, between regions and between countries.
Because interdependence is its basis, economics is necessarily a study of systems; because it is concerned with the allocation of resources by human beings, it is a study of decision-making systems. (As we shall see, this does not necessarily imply a study of the process of decision-making; micro-economists have generally been concerned with consequences rather than processes.) Economists have therefore to cope with two intrinsic difficulties of system analysis - the definition of system boundaries and the specification of system structure. On the one hand, all economic systems are sub-systems - sub-systems both of larger economic systems (unless one is explicitly dealing with the world economy) and also of more broadly defined human and ecological systems; thus interdependencies transcend the bounds of the
1. A version of this paper was presented at the Annual Conference of the Association of University Teachers of Economics at Canterbury on April 6, 1971.
2 T. S. Kuhn, The Structure of Scientific Revolutions (Chicago: University of Chicago Press, 1962).
system being studied. On the other hand, some abstraction from detail is essential, and this involves not only the omission of variables, but also distortion of the relationships which are included. Thus the economist has no option but to construct models which fall short - usually far short - of a complete specification of the system which he wishes to analyse; he must choose where to make his approximations, some of which must normally be very drastic. It follows, first, that no economic model can be finally judged by the resemblance between its specification and the real-life system which it claims to represent; and, second, that the choice of different specifications by different economists for their models of the same system carries no presumption that one of them must be in error. For these reasons, it is safer to talk of the “sufficiency” of models than of their “realism.”
Though approximations in both directions are necessary, economists tend either to jettison detail in order to concentrate on major interactions, or to ignore interdependencies in order to concentrate on relative detail. This, of course, is the basis of the distinction between macro-economics and micro-economics. Macro-economics explores the system known as the national economy, defined into such sectors as consumption, investment, government expenditure and exports, each of which is a highly complex sub-system. The export sector necessarily implies interdependence with other national economies: this interdependence may be handled very crudely - even ignored - or analysis may concentrate, in international trade theory, on the intersections of these national economy sets. Sometimes the components of the national economy will be defined, for the purposes of input-output analysis, as industry groups - which are not proper sub-sets of the major sectors normally used in macro-economic analysis. Whatever the form of the macro-level analysis, the sub-systems of which it is composed are treated very simply by the use of assumptions which may be rejected in the analysis of the sub-systems themselves. (For example, theoretical international trade usually appears to be carried on under conditions of universal perfect competition, while the industries analysed in input-output analysis may operate with both constant marginal costs and constant returns to scale.) But, because of the fundamental difficulties of system analysis, such a conflict of assumptions at different levels cannot invalidate the arguments which rest on them.
Micro-economics, on the other hand, simply assumes away some of the interdependencies which form the subject-matter of macro-system analysis. But this obvious contrast with macro-economics should not be allowed to obscure the fact that micro-economics makes its sacrifices of detail too; and they can be very large. For, although it claims to include within its scope the allocation of a firm’s internal resources, it regards the firm itself as the basic decision-making unit. Since, however, the greater part of resource allocation within industry is determined nowadays by firms which are themselves decision-making systems, a third level of analysis is possible, which is
likely to require further sacrifice of interdependencies in order to explore the details of sub-system behaviour. The economics of organisational behaviour not only illuminates the affinities between economics and organisation theory; it is a natural extension of the scope of the subject, being characteristically concerned with the relationship between structure and performance - the ways in which the system being studied responds to and regulates choice.
This emphasis on a systems study necessarily implies some qualifications to the view sometimes expressed that economists should seek to emulate as closely as possible the methodology of the experimental sciences.  Since this methodology has traditionally rested on the isolation and manipulation of closely-specified relationships, it presents difficulties for the economist, whose manipulation must usually be statistical (possibly with the number of trials outside his control), and who frequently cannot isolate the phenomena which he wishes to study. But not only is narrow isolation difficult; it is often inappropriate. For it is characteristic of system behaviour that it may not be explicable as a simple - or even weighted - sum of separate effects. From this point of view, it is the contrast, not the comparison, between economics and experimental science which is illuminating.
There are greater similarities between economics and applied science, especially science directed towards the development and operation of industrial processes. For these are systems too, and systems normally too large to be modelled in full. So the scientist is here faced with a problem akin to that of the economist: to choose a degree of abstraction in his experimentation which is drastic enough to simplify his analysis and yet robust enough to give value to his conclusions. For such choices his academic training in experimental method does not prepare him very well. “The transition from the laboratory to plant implies a change of scale from what can, in most cases, be handled and controlled manually by one scientist, to a system which is far outside the capacity of one man, unaided by automation and instrumentation, to control. Many scientists, we find, have a very hazy idea of the sort of problems that arise on transferring operations from laboratory to plant.”  But awareness of such problems is necessary if the laboratory experiments performed are to be those which are most relevant.
However, although the unrealistic assumptions of the economist may be fairly compared with the artificial environment of the laboratory as a means of abstracting from complex systems, yet it should not be overlooked that the
1. E.g., R. G. Lipsey, An Introduction to Positive Economics, Second edition (London: Weidenfeld & Nicolson, 1966), Chapter 1.
2. A. Baines, F. R. Bradbury and C. W. Suckling, Research in the Chemical Industry (London: Elsevier, 1969), p. 165. Their example of filtration suggests some analogies in economic policymaking.
character of the abstraction is different. The scientist abstracts from complexities towards the detail of real phenomena; the economist tends to abstract from detail into terms which have only economic meaning. 
There is a further difficulty in the way of general reliance on experimental or statistical-experimental method in economics. Not only may hypotheses be difficult to test, or relate to system behaviour to which closely restricted analysis is not appropriate; some economic hypotheses turn out not to be hypotheses at all, but paradigms.
A paradigm, in the natural sciences as well as in economics, defines the type of relationships to be investigated and the methods and abstractions to be regarded as legitimate within a particular problem area.  Once such terms of reference are generally accepted by practitioners within that area, research becomes “a strenuous and devoted effort to force nature into the conceptual boxes supplied by professional education.”  (All boxes are empty until the work of filling them begins.) A paradigm must therefore be both comprehensive and open-ended; it leaves many problems to be solved and holds out the prospect of successful solutions to those who formulate and test with skill and care particular hypotheses consistent with the paradigm. For the natural scientist, at least, therefore, it offers “a criterion for choosing problems that, while the paradigm is taken for granted, can be assumed to have solutions.”  That such criteria are indispensable for the natural scientist is emphasised by P. B. Medawar, explaining “why scientists seem so often to shirk the study of really fundamental or challenging problems... No scientist is admired for failing in the attempt to solve problems that lie beyond his competence. The most he can hope for is the kindly contempt earned by the Utopian politician. If politics is the art of the possible, research is surely the art of the soluble. Both are immensely practical-minded affairs.” 
H. A. Simon applies a similar argument more widely. “People (and rats) find the most interest in situations that are neither completely strange nor entirely known - where there is novelty to be explored, but where similarities and programs remembered from past experience help guide the exploration. Nor does creativity flourish in completely unstructured situations. The almost unanimous testimony of creative artists and scientists is that the first task is to impose limits on the situation if the limits are not already
1. Cf. R. M. Cyert and E. Grunberg, “Assumption, Prediction and Explanation in Economics,” in R. M. Cyert and J. G. March, A Behavioural Theory of the Firm (Englewood Cliffs, N.J.: Prentice-Hall, 1963), pp. 301-2.
2. Kuhn, op. cit., pp. 10, 11.
3. Kuhn, op. cit., p. 5.
4. Kuhn, op. cit., p. 37.
5. P. B. Medawar, The Art of the Soluble (London: Methuen, 1967), pp. 86-7.
given.”  It is the role of the paradigm to provide such limitations to the agenda for inquiry.
Because a paradigm defines a set - often a very large set - of possible hypotheses, but makes no claims for the validity of any particular members of that set (some of which, indeed, will be mutually exclusive alternatives), it follows that paradigms, unlike the hypotheses to which they give rise, cannot be validated by experimental or statistical methods. Failure to recognise this distinction has led to much unnecessary argument, of which the disputes over profit-maximisation provide a notorious example. For profit-maximisation is not a hypothesis but a paradigm; and whereas a specific hypothesis embodying some version of profit-maximisation can, in principle, be tested, the paradigm of profit-maximisation cannot. Only in long-period static equilibrium with perfect knowledge is its formulation unique; and no such experimental conditions can be found. One common form of criticism is, in fact, a tribute to its virtue. With a little ingenuity, it is possible to explain almost any kind of business behaviour as profit-maximisation. The retort that, “if it can explain everything, it explains nothing” would be conclusive against a loosely formulated hypothesis; but it is precisely this ability to generate a variety of hypotheses to explain, if not everything, yet a large body of important phenomena, which is the essential virtue of a paradigm. Lipsey’s attempt to emphasise the testing of economic predictions suffers from a similar confusion: the theory expounded in his text-book is necessarily a paradigm, to which his proposed tests, being designed for hypotheses, cannot properly be applied. 
The obverse of a paradigm’s continued fertility is the continued existence of unsolved problems. A paradigm which left no issues unresolved would be useless as a guide to further work. Thus “a thousand difficulties do not make one doubt”  concerning the acceptability of a paradigm; on the contrary they offer a thousand opportunities for the deployment of professional skill. Provided that they are being steadily resolved, the existence of difficulties is a symptom, not of a paradigm’s weakness, but of its continuing strength. This remains true even when some major difficulties prove recalcitrant. For example, attempts to explain the path of the moon by the application of Newtonian theory failed consistently for sixty years; yet there were no serious proposals for the rejection of Newtonian theory. What was in question was not the paradigm, but the professional skill of the scientists who had failed to derive an appropriate hypothesis from it; and, in the event, confidence in Newtonian theory was justified. 
1. H. A. Simon, The Shape of Automation for Men and Management (New York: Harper & Row, 1965), pp. 97-8.
2. Lipsey, op. cit., e.g., Chapter 29.
3. J. H. Newman, Apologia Pro Vita Sua.
4. Kuhn, op. cit., pp. 39, 81.
It is not, therefore, surprising, that a paradigm, once established, should prove difficult to overthrow. Since its continued usefulness depends on the double condition of unresolved problems and good prospects of their eventual solution by the application of the paradigm, there can be no unequivocal standard by which a paradigm can be judged to have failed. Those who attack a paradigm may simply be confessing their inability to use the tools of their trade as effectively as their fellows. Even if this is not an effective deterrent, to discard a well-established paradigm is to discard an important part of one’s apparatus for recognising and solving problems. Furthermore, since a paradigm, like a management control system, provides the basis for selecting both problems and the relevant variables to be investigated, it may condition its users against even the perception of some of the more fundamental threats. An experiment in which subjects readily identified as normal wrongly coloured playing cards inserted into an otherwise normal pack provides some formal confirmation of the common experience in, all manner of contexts that observations are “fitted to one of the conceptual categories prepared by prior experience.”  A paradigm produces intellectual tunnel vision.
Thus something quite exceptional in the way of difficulties must become apparent before an established paradigm can be seriously challenged. As Shackle says, “Theoretical advance can spring only from theoretical crisis.”  In the natural sciences, at least, the existence of a rival paradigm is a necessary condition for a challenge - no paradigm which offers some answers is going to be abandoned unless alternative answers are on offer. But it is certainly not sufficient. The clearest evidence for this statement is provided by the anticipations of later major developments to be found, not in the underworld of economics, but in the intendedly definitive text of Marshall’s Principles.  Until the definitiveness of Marshall was challenged, these anticipations lay not only undeveloped but often unnoticed.
Shackle’s own explanation of the persistence of paradigms can be summarised in his own words. “The chief service rendered by a theory” - by which he clearly means a paradigm, not a hypothesis – “is the setting of minds at rest. So long as we have a satisfying conceptual structure, a model or a taxonomy which provides for the filing of all facts in a scheme or order, we are absolved from the tiresome labour of thought, and the uneasy consciousness of mystery and a threatening unknown.”  This explanation is
1. Kuhn, op. cit., pp. 62-4; the experiment is reported in J. S. Bruner and L. Postman, “On the Perception of Incongruity: A Paradigm,” Journal of Personality, Vol. XVIII, 1949, pp. 206-23.
2. G. L. S. Shackle, The Years of High Theory (Cambridge: Cambridge University Press, 1967), p. 288.
3. A convenient selection of examples may be found in D. H. Robertson, “A Revolutionist’s Handbook,” reprinted in Utility and All That and Other Essays (London, Allen and Unwin, 1952), pp. 66-80.
4. Shackle, op. cit., p. 288.
in part misleading. To see why, it is necessary to distinguish between unease and hard thought. Paradigms, far from avoiding the labour of thought, may call for both intense and protracted effort if they are to be expressed in viable hypotheses.  Their virtue, in this respect, lies in permitting that effort to be deployed within a well-defined structure, instead of having to be applied to the definition of that structure; they permit a concentration on short-run questions. But in academic work, as in business, long-run questions, even if no more intellectually taxing, are much less comfortable, because they tend to open up an unpalatable range of options. They require the managing director to consider what business he should be in, or the academic the proper scope of his subject. An acceptable paradigm affords protection from such disturbing speculations.
“Theory... imposes a beautiful simplicity on the unbearable multiplicity of fact, gives comfort in face of the unknown and unexperienced, stops the teasing of mystery and doubt which, though salutory and life-preserving, is uncomfortable, so that we seek by theory to sort out the justified from the unjustified fear. Theories by their nature and purpose, their role of administering to a ‘good state of mind,’ are things to be held and cherished. Theories are altered or discarded only when they fail us.” 
Intellectual retooling is uncomfortable, as well as expensive.
This argument needs to be taken just one stage further, in order to explain the tenacity with which people cling to old paradigms even in crisis, and even when alternatives are available. Often the new contender is not a perfect substitute for the old: while offering solutions to some difficulties which appear insoluble within the established paradigm, it may offer inferior solutions to others; and, indeed, to some questions hitherto satisfactorily handled it may offer no solution at all. For example, Lavoisier, in offering a solution to the critical issues which the phlogiston theory seemed unable to resolve, could provide no explanation whatever for the similarities between metals, which phlogiston theory had readily accounted for. 
Thus the competition between paradigms turns not simply on their relative merits in explaining certain important phenomena, but on judgments about which are the important phenomena to explain. For these judgments there are no generally acceptable criteria; indeed they cannot be made without excursions into those regions of mystery and doubt from which paradigms, once accepted, serve to protect us. A change of paradigm redefines the set of relevant problems, and the criteria for selecting problems and evaluating solutions: it changes to some degree - occasionally to a large degree - the accepted definition of the scope of a subject. With its combination of the threatened obsolescence of some established methodology,
1. Kuhn, op. cit., pp. 26, 30.
2. Shackle, op. cit., pp. 288-9.
3. Kuhn, op. cit., p. 147.
and the posing of awkward, sometimes fundamental, questions about the nature of a subject, a time of paradigm change is a time of upheaval that for many may be more disturbing than exhilarating. A subject in which paradigms are often not firmly-established, like economics, offers much less security to its practitioners than one, like chemistry, in which they are relatively secure. (Graduate chemists turning to economics for the first time are liable to be disconcerted by this loss of security.) But even apparently-assured security can prove illusory, as atomic physicists have painfully realised in recent years.
Whether economics (or any other social science) has yet succeeded in establishing any paradigms as widely accepted, even for a short time, as those associated with Copernicus, Newton or Lavoisier, may be doubted. Nevertheless, the concept of paradigm change seems capable of extension to illuminate some major innovations in economic theory. It has, indeed, recently been effectively used by Axel Leijonhufvud in his examination of the Keynesian revolution.  Leijonhufvud argues that the neo-classical synthesis has been achieved by forcing Keynes’ ideas within the traditional general equilibrium paradigm of a static system of simultaneous equations; and that Keynes’ attempt to construct a new paradigm, emphasising processes and information flows within the system, has been rejected, or even unrecognised. This argument will not be further considered in this paper, except for drawing a later analogy with behavioural theory; attention will be concentrated on micro-economics, beginning with the emergence of the theory of the firm.
The Marshallian synthesis on the theory of value was constructed with almost incredible care and subtlety; indeed some of the sharpest minds of the twenties and thirties simply failed to appreciate what Marshall had done, and construed his caution as hesitancy and his subtlety as confusion. But Marshall was facing methodological difficulties which could not be solved, only lived with. Shackle partially explains the situation. “Marshall’s self-imposed endeavour was an intensely difficult one. He sought to describe a mechanism of evolution of the firm and industry; to derive the principles of this mechanism from the detailed and wide observation of a segment of British economic and social history,... and to make his account of this observable productive evolution the vehicle of laws which should be in some degree general and permanent.” 
Shackle places the emphasis on the problem of explaining a great variety of specific facts by a single body of theory - the achievement of a high level
1. Axel Leijonhufvud, On Keynesian Economics and the Economics of Keynes (New York and London: Oxford University Press, 1968). I am indebted to Professor A. D. Bain for drawing my attention to the significance of this work.
2. Shackle, op. cit., p. 44.
of abstraction without significant loss of sufficiency. This type of problem, as was pointed out earlier, is characteristic of all science, though of peculiar difficulty in this particular instance. But the way Marshall tackled the problem evoked a difficulty of a special sort. The key lies in Shackle’s phrase “a mechanism of evolution.” Mechanism suggests mathematics; and it was not surprising that Marshall, a mathematician himself should turn to mathematics for a formal exposition of “general and permanent laws.” If a formal mathematical model was to be produced, then the obvious - perhaps the only possible - body of theory to use was the differential calculus, the value of which in economics had first been effectively demonstrated by Cournot. But an analytical method based on differential calculus, though the best available, was hardly ideal as a paradigm of growth and change. Marshall consistently emphasised biological analogies, but there was simply no “biological mathematics” adequate for his purpose; and so evolution had to be explained in terms of static equilibrium. The use of a strictly timeless theory by one who was so conscious of the importance of time represents a heroic - and highly successful - use of abstraction; but only by the use of all Marshall’s care and subtlety could it be made to appear convincing. It may, indeed, be judged too successful and too convincing; for whereas Marshall was keenly aware that his mathematical abstractions would lose sufficiency if pressed much further, some of his successors, being young and bold, were less inhibited. By revealing the inherent contradictions between the model and the real world, which Marshall had so skillfully concealed, they helped to precipitate a crisis in value theory.
The theoretical argument was forcefully summarised by Sraffa in his famous article of 1926, in which he demonstrated that increasing and decreasing returns were both strictly incompatible with other assumptions of the standard formal analysis, that the size of the firm was therefore left indeterminate by this analysis, and that there was thus no adequate justification for casting that analysis in terms of perfect competition.  The logic of Sraffa’s criticism and of his proposed solution are worth examining. The key sentences run as follows.
If diminishing returns arising from a ‘constant factor’ are taken into consideration, it becomes necessary to extend the field of investigation so as to examine the conditions of simultaneous equilibrium in numerous industries: a well-known conception, whose complexity, however, prevents it from bearing fruit, at least in the present state of our knowledge, which does not permit of even much simpler schemata being applied to the study of real situations. If we pass to external economies, we find ourselves confronted by the same obstacle, and there is also the impossibility of confining within statical conditions the circumstances from which they originate.
1. P. Sraffa, “The Laws of Returns under Competitive Conditions,” Economic Journal, Vol. XXXVI 1926, reprinted in G. J. Stigler and K. E. Boulding (eds.), Readings in Price Theory (London: Allen and Unwin, 1953), pp. 180-97.
It is necessary, therefore, to abandon the path of free competition and turn in the opposite direction, namely towards monopoly. Here we find a well-defined theory in which variations of cost connected with changes in the dimensions of the individual undertaking play an important part.” 
These sentences are perhaps so familiar that it will be easier to analyse the argument if they are paraphrased. The strict formal requirements of static partial equilibrium analysis do not permit the conditions which are logically necessary for the existence of perfect competition. Therefore something must go. The cost conditions which make perfect competition possible are indeed compatible with dynamic general equilibrium; but general equilibrium is a much less usable paradigm than partial equilibrium, and dynamic analysis is still more hopeless. On the other hand, the theory of monopoly offers a readily-available alternative to perfect competition, while still retaining all the usual conditions of static partial equilibrium.
Thus the argument turns, not on the existence of perfect competition as a recognisable state of affairs, but on first, the internal consistency, and second, the relative usefulness, of competing paradigms. It is important to take these two criteria, of internal consistency and relative usefulness, separately; and it is convenient to begin with the latter.
Let us accept for the moment Kaldor’s conclusion that “long-period static equilibrium and perfect competition are incompatible assumptions.”  Marshall’s theory made room for monopoly; the new theory had no room for perfect competition, as Joan Robinson forcefully made clear. When we see some situations approximating to perfect competition, but none, in developed economies, approximating to long-period static equilibrium, what are we to think of a choice of paradigm in which perfect competition becomes an inadmissible market form? Surely the answer is that the choice was soundly based on good scientific practice, which exemplifies at this point the economic doctrine of opportunity cost. Usefulness, rather than immediate realism, is the proper ground for choosing between paradigms. The cost of giving up static partial equilibrium analysis, in terms of existing theory to be discarded, was far higher than the cost of giving up perfect competition, and the gains, in terms of alternative theory lying ready for exploitation, were far less.
That this is the relevant basis for choice is confirmed by the reasoning of the most distinguished economist who made the opposite choice, in favour of general equilibrium theory - J. R. Hicks. He stood Sraffa’s conclusion
1. Sraffa, op. cit., p. 187.
2. N. Kaldor, “The Equilibrium of the Firm,” Economic Journal, Vol. XLIV (1934); reprinted in N. Kaldor, Essays on Value and Distribution (London: Duckworth, 1969), p. 46.
on its head: imperfect competition was incompatible with partial equilibrium, general equilibrium was incompatible with anything other than perfect competition. The essentials of Hicks’ argument, too, are worth quoting in his own words. 
It has to be recognised that a general abandonment of the assumption of perfect competition, a universal adoption of the assumption of monopoly, must have very destructive consequences for economic theory. Under monopoly the stability, conditions become indeterminate; and the basis on which economic laws can be constructed is therefore shorn away…
It is, I believe, only possible to save anything from this wreck - and it must be remembered that the threatened wreckage is that of the greater part of general equilibrium theory - if we can assume that the markets confronting most of the firms with which we shall be dealing do not differ very greatly from perfectly competitive markets... At least, this get-away seems well worth trying. We must be aware, however, that we are taking a dangerous step, and probably limiting to a serious extent the problems with which our subsequent analysis will be fitted to deal. Personally, however, I doubt if most of the problems we shall have to exclude for this reason are capable of much useful analysis by the methods of economic theory.
No more than Sraffa, Kaldor, and the others who argued the opposite case, does Hicks appeal to facts. Indeed, he admits that the facts may well be against him. Neither party follows Beveridge’s prescription, endorsed by Lipsey, to seek empirical verification.  And on this issue they are right, and Beveridge and Lipsey are wrong. For the argument is not about hypotheses - concerning which Beveridge and Lipsey are of course quite correct - but about the kinds of hypotheses and the kinds of data that might be presented for verification; and here the empiricist’s prescription is not only inappropriate but often impossible.
The readiness with which Hicks is prepared to accept the exclusion of important problems from consideration as the price of using the paradigm of perfect competition should also be noted. The availability of a paradigm is more relevant than the importance of a problem. Here again Hicks is following scientific principles, as explained by Medawar. “Good scientists study the most important problems they think they can solve. It is, after all, their professional business to solve problems, not to grapple with them. The spectacle of a scientist locked in combat with the forces of ignorance is not an inspiring one if in the outcome, the scientist is routed.”  Economists are perhaps in general readier than natural scientists to tackle ignorance with inadequate weapons; but this readiness springs from inferior armament rather than superior virtue. And it is, after all, only relative; it would be difficult to maintain that the distribution of economic effort
1. J. R. Hicks, Value and Capital (Oxford: Oxford University Press, 1939), pp. 83-5.
2. Lipsey, op. cit., pp. xi-xii, 3-18.
3. Medawar, op. cit., p. 7.
reflects at all closely the importance of economic issues; much less difficult to relate it to the availability of usable paradigms. Nor is this necessarily wrong, for it can be argued that a discipline will make faster progress if its practitioners are insulated from pressures to “choose problems because they urgently need solution and without regard for the tools available to solve them.” 
So far we have argued that, given the existence of a crisis in value theory, the solution of abandoning perfect competition, though apparently odd, was justified. But we still have to ask, was there a real theoretical crisis? If one accepts the earlier argument about the significance of paradigms, and, particularly, the argument about the degree of abstraction - in structure as well as in the choice of variables - required to create a usable paradigm in a study of such complex systems, the answer must surely be no. The theoretical crisis arose out of a misconception about the nature of the subject, and therefore of the way it should develop. Any usable model must be a mis-specification of the reality to which it refers; in economics this mis-specification must often be so great as to show little apparent resemblance to that reality. To refine the abstractions in a workable paradigm is often to refine away the reality that remains; consistency must often be sacrificed in order to retain adequate sufficiency. When the conditions requisite for static partial equilibrium analysis are carefully spelt out, as they were for example by Kaldor in 1934,  it should become obvious that long-period static equilibrium is formally incompatible not merely with perfect competition, but with any of the real-world phenomena which we habitually use it to explain. Not even the simplest curve shifting is logically permissible: as Mrs. Robinson has sardonically observed, equilibrium is not a position at which one can arrive; one must be in it already. 
Thus “a more rigorous formulation of the conditions under which it is possible to make generalisations about the factors determining economic equilibrium”  must be no more than a subsidiary concern, since it is obvious that the conditions will never be met. What matters is how extensively they can be violated without seriously impugning the result to which they lead. A strict regard for internal consistency in economic theory is as likely to be a vice as a virtue.
Therefore before deciding whether she took the “wrong turning” in writing The Economics of Imperfect Competition instead of “abandoning static
1. Kuhn, op. cit., p. 163.
2. N. Kaldor, “The Determinateness of Static Equilibrium,” Review of Economic Studies, February 1934; reprinted in Essays on Value and Distribution, pp. 13-33.
3. J. Robinson, Collected Economic Papers, Vol. II (Oxford: Blackwell, 1966), p. 120.
4. Kaldor, Essays, p. 13.
analysis and trying to come to terms with Marshall’s theory of development,” Mrs. Robinson ought first to have enquired a little more carefully whether any turning was needed at all. Simply to state that “the profound inconsistency between the static base and the dynamic superstructure had become too obvious” just will not do.  Nor will the more recent argument that “imperfect competition came in to explain the fact, in the world around us, that more or less all plants were working part time:”  the phenomena of short-run general disequilibrium cannot be explained in terms of long-run partial equilibrium.
Are we then, as D. H. Robertson suggested, no more than half in jest, “to regard all that has happened since (Marshall) in this field as a vast crime wave”?  Surely not; for two reasons. The less important reason is that the changing structure of industry did pose problems of fact which appeared to reinforce the problems of theory; any commentary on the arguments of the time which ignores the contemporary concern with these problems must appear unfair to some of the protagonists of change, even though one may doubt the completeness of their success in explaining the new structure by the new theory. The more important reason is that, as is likely to happen when a paradigm changes, the new theory redefined the scope of this branch of economics. As Shackle observes, “not only the answers, but the questions, were new. The whole notion of what value theory sought to do and the way its aim should be accomplished had been changed... Primacy had passed from the autonomously self-subsisting technical commodity to the firm considered as a profit-maximising policymaker. . The creation of the theory of the firm brought the analysis of decision-making within the accepted scope of the subject; it thus not only made possible the development of managerial economics, but determined its characteristic virtues and defects.
The almost simultaneous appearance of two full-length presentations of the new theory of the firm by E. H. Chamberlin and Mrs. Robinson necessarily raised the question whether it was indeed one theory or two. But the question was apparently soon disposed of: although Chamberlin continued to insist, to the end of his life, on the fundamental differences between the concepts of monopolistic and of imperfect competition, very few economists of importance, even among those most sympathetic to Chamberlin’s formulation, took the claim seriously.  This was unfortunate, because Chamberlin was quite right.
1. J. Robinson, Collected Economic Papers, Vol. 1 (Oxford: Blackwell, 1951), pp. vii-viii.
2. J. Robinson, The Economics of Imperfect Competition, Second Edition (London: Macmillan, 1969), p. vi.
3. Robertson, op. cit., p. 73.
4. Shackle, op. cit., p. 65.
5. Shackle, op. cit., p. 62.
The trouble may be explained as a confusion between hypothesis and theory. Much of the formal analysis, notably the tangency solution which reconciles monopolistic discretion over price with normal competitive profits, can indeed be regarded as common to both. But these similarities can be explained by the natural inclination to use and develop familiar tools of analysis within the accepted framework of partial equilibrium and profit-maximisation; the function of the analysis, in relation to both theoretical issues and their views of the world, is very different for the two authors.
Imperfect competition was created to escape from the dilemma propounded by Sraffa. Since rising costs were excluded by the formal conditions of perfectly competitive partial equilibrium (as well as apparently absent from many firms), and yet the method of partial equilibrium analysis seemed indispensable, the only escape seemed to lie in a falling demand curve for the individual firm. This falling demand curve was not an observed fact, but - most compelling of arguments - a methodological necessity. As P. W. S. Andrews observed, “Seen from this methodological point of view, Joan Robinson’s demand functions have no analytical roots. Her demand curves fall simply because she tells them to do so.”  Indeed, she was inhibited from looking for analytical roots by her concern to preserve the concept of the industry, which led her to regard the products of competing firms as virtually identical in all respects save the attitudes of individual customers towards them, and thus eliminated any rational basis for the falling demand curves which her theory required.
Such abstractions may well be justified by the usefulness of the theoretical structure which they make possible (and some such concept as the industry is essential to partial equilibrium analysis); but there is a danger that inferences about the real world may be drawn from theoretical assumptions, instead of the reverse. And of course in this instance such inferences were drawn, most conspicuously by Mrs. Robinson herself. For example, the section headed “Forms of Competition” in her article “Imperfect Competition Revisited” lays overwhelming emphasis on competitive waste.  In addition, the excess capacity and unexhausted economies of scale which were presented as such notable consequences of the theory were already explicit in the assumption of falling costs on which it was founded. The moral of imperfect competition is that potential economies of large-scale production are frustrated by producers’ iniquity and consumers’ gullibility or perversity; the situation therefore seems to demand, rather than permit, “almost unlimited pushing around.”  But this is not the only theory which fits the formal analysis.
1. P. W. S. Andrews, On Competition in Economic Theory (London: Macmillan, 1964), p. 22.
2. J. Robinson, “Imperfect Competition Revisited,” Economic Journal, September 1953, reprinted in Collected Economic Papers, Vol. II (Oxford: Blackwell, 1960), pp. 228-9.
3. Robertson, op. cit., p. 75.
Chamberlin, by contrast, started not with costs but with demand, which reflected differences in consumers’ preferences and between competitive products. His assumption of uniform demand and cost curves is much more obviously a temporary expedient to aid exposition than it is in Mrs. Robinson’s analysis, and the tangency equilibrium is not presented as a general solution. Because products and consumers do differ, even in equilibrium “some (or all) of the demand curves may lie at various distances to the right of the point of tangency, leaving monopoly profits scattered throughout the group - and throughout the price system.”  We should therefore be much less surprised than even the sympathetic D. H. Robertson to find Chamberlin speaking of his equilibrium - monopoly profits and all - as a sort of ideal.  If economies of scale are frustrated in this paradigm, it is largely because the alternative is to frustrate the need for variety which flows from “ differences in tastes, desires, incomes, and locations of buyers, and differences in the uses which they wish to make of commodities.”  But perhaps Chamberlin did not take his falling cost curves too seriously. After all, they were a methodological necessity, given a falling demand curve, for equilibrium with normal profits, just as falling demand curves were a methodological necessity, given falling costs, for Mrs. Robinson.
The distinction between imperfect and monopolistic competition is perhaps especially marked in the area of managerial economics. The concepts of monopolistic competition harmonise readily with the emphasis in marketing theory on the profit opportunities in offering distinctive consumer satisfactions, as evaluated by the consumer. To the marketer, as once to the economist, the customer buys, not a product, but the expectation of benefits: the variety of ways to consumer satisfaction, and the importance of consumer satisfaction, both submerged by the tendency of imperfect competition theory to regard every means by which a firm may aim to give added value as a wasteful device for bamboozling the ignorant customer, are fundamental assumptions of monopolistic competition. In the current management jargon, imperfect competition is producer-oriented, monopolistic competition is consumer-oriented.
Furthermore, monopolistic competition theory, though formulated in terms of static partial equilibrium for the single-product firm, has adequate sufficiency to handle in a modest way questions of product-line policy, new-product pricing, and the exploitation of the product life cycle. Even innovation can be treated in terms of competitive strategy - but not if one confuses monopolistic with imperfect competition. B. R. Williams’ complaint against economists’ treatment of competitive pressure is justified, but his
1. E. H. Chamberlin, The Theory of Monopolistic Competition (Cambridge, Mass.: Harvard University Press, 1933), p. 113.
2. Robertson, ibid.
3. Chamberlin, op. cit., p. 214.
explanation is not quite right. “Whether, and in what way, competition stimulates... innovation,” writes Williams:
is a problem foreign to static theory, though in fact static theory has exercised a very strong influence on economists’ approach to dynamic problems. Thus, examples of product differentiation are generally drawn from the market for consumer goods and stress brand differences in fields like cereals and cosmetics. When, however, we take examples such as aircraft engines, electronics, man-made fibres, and pharmaceuticals, we face the significant possibility that product differentiations may not be ‘market imperfections’ in the static sense, but an inevitable part of the process of man-made innovations required for the efficient pursuit of economic growth. 
Of course static theory is strictly inconsistent with change of any kind, even the introduction of a different packet for an unchanged product. But once we reject the hobgoblin of consistency,  we find comparative statics a useful method of handling change. The cause of the trouble is less the static formulation of the models than the assumption of imperfect competition theory that product differentiation produces waste, not progress. Novelty is undesirable because it impedes mass-production. Monopolistic competition, on the other hand, does allow us to ask whether mass-production may be undesirable because it impedes novelty.
If monopolistic competition is both so different and in some ways so superior to imperfect competition, why have the two been treated as so nearly synonymous? Part of the explanation, as given before, is that the central analysis appeared so similar that almost everyone assumed the theories to be similar also. It is still necessary to explain why the assimilated theory looks so distinctly Robinsonian; but that is easy. The theory of value was apparently in a state of crisis, and Mrs. Robinson’s book appeared as the culmination of a painful and difficult struggle to resolve it, in which many of the keenest economic minds had publicly engaged. The urgency and difficulty of that struggle made impossible the perception of Chamberlin’s work in any other way than as a solution to the crisis. Its entirely different origins, being neither a common concern nor well-publicised, aroused no interest whatsoever. The saddest part of this paradox is that, had there been no crisis, Chamberlin’s book would have received far less attention, because it would have met no apparent need. The tragedy of Chamberlin’s professional life is that if he had not spent so much of his time and energy protesting the distinctiveness of his theory, he would probably have spent that time and energy protesting its importance.
1. B. R. Williams, Technology, Investment and Growth (London: Chapman & Hall, 1967), p. 83.
2. “A foolish consistency is the hobgoblin of little minds, adored by little statesmen and philosophers and divines.” R. W. Emerson, Essays.
By setting out to show that “the analysis of the output and price of a single commodity can be conducted by a technique based upon the study of individual decisions,”  Mrs. Robinson for the first time appeared to bring decision-making by the competitive firm within the ambit of empirical economic research. That the definition of such an important new field failed to precipitate a flood of investigations, as one would expect in the experimental sciences, was probably largely due to the feeling that research was unnecessary since facts could apparently be deduced from purely geometrical arguments. There certainly do not seem to have been any immediate doubts that the new theory offered an adequate description - or prescription: it was not always clear which - of actual business behaviour. Thus the report of the first serious investigation (the Oxford inquiry)  that businesses did not behave in this way inevitably caused some consternation; the paradigm has been in a kind of crisis ever since.
Many typical features of a paradigm crisis have been visible. There has been no general agreement on the terms of reference for the debate, nor indeed on the precise scope of paradigm under attack. Nor has the attack been well co-ordinated: P. W. S. Andrews, the only economist to develop both a full-scale critique and an alternative paradigm, published the two halves of his argument fifteen years apart, and in the wrong sequence for maximum effect.  On the opposing side, many of the successful revolutionaries, quite properly, turned conservative to protect the newly-established paradigm; and their defence owed little to empirical evidence about firms’ pricing behaviour.
Such disregard for empirical evidence, it was argued earlier, is generally appropriate in a conflict of paradigms; and it is particularly appropriate in this instance. For Mrs. Robinson’s theory was based not, as she claimed, on “the study of individual decisions,” but on the conditions of individual equilibrium, just as perfect competition had been; and both perfect and imperfect competition are empty of predictions about the ways in which firms actually fix prices. Andrews saw more clearly than most that the dispute turned on questions not of behaviour but of structure: whether the model should assume atomistic competition or oligopoly, and whether it should be formulated in terms of equilibrium. Part of Andrews’ critique offers a remarkable parallel to Sraffa’s earlier argument; whereas Sraffa had shown that a strict interpretation of the conditions of long-period static partial equilibrium virtually excluded increasing costs for the individual firm. Andrews now argued that these conditions also excluded falling demand
1. J. Robinson, The Economics of Imperfect Competition (London: Macmillan, 1933), p. 15.
2. R. L. Hall and C. J. Hitch, “Price Theory and Business Behaviour,” Oxford Economic Papers, No. 2, 1939.
3. P. W. S. Andrews, Manufacturing Business (London: Macmillan, 1949), and On Competition in Economic Theory (London: Macmillan, 1964).
curves for the individual firm.  Thus we reach the final condemnation of long-period static partial equilibrium: it is incompatible first, with perfect competition, second, with real-world phenomena, and finally, even with itself.
This rejection of equilibrium theory did not worry Andrews, who had previously developed an alternative paradigm, in which a “steady state” of uniform prices is determined by competition within an industry, and each firm’s market share depends on dynamic considerations of goodwill; but, as he acknowledged, it worried other people.  For it is the concept of equilibrium which is at the heart of the crisis; and the abandonment of equilibrium is a much more fundamental change than that implied by the creation of the theory of the firm, which was developed, in accordance with Sraffa’s advice, precisely in order to preserve the static equilibrium method of analysis. Micro-economists need a theory of the firm; and for some purposes the marginalist equilibrium theory is the best theory we have.
How, then, is the paradigm defended? Andrews’ critique, though in its own terms irrefutable, is unacceptable; it has therefore apparently been ignored. Perhaps economists have learned to be less impressed by revelations of inconsistency in their theoretical assumptions, and accept that Andrews’ criticisms are no more valid than were Sraffa’s. Expositions and explanations of business behaviour which conflict with micro-equilibrium theory, however, have met with vigorous onslaughts, in which the terms of the argument, as is usual in controversies over paradigms, have been defined in a way that comes near to ensuring success. Equilibrium theory is justified by assuming its validity. Rationality is equated with profit maximisation, which in static equilibrium implies mathematically the equality of marginal cost and marginal revenue; therefore any business observed violating the theory is behaving irrationally, and any alternative theory must assume irrationality, which, as we all know, makes theorising impossible - unless, of course, it be the consumer irrationality which is the not-quite-explicit basis of imperfect competition. Even Cohen and Cyert, who might be expected to be particularly sensitive to this issue, discuss decision-making by marginal analysis as if this were synonymous with rationality.  Andrews’ own theory has inevitably come in for particularly harsh treatment, and it has unfortunately been too easy to assume that the obscurity of his style reflects confusion in his thought; but the standard accusation that he is rejecting profit-maximisation, rather than equilibrium (which persists even in Silberston’s recent survey)  simply indicates the confusion of his critics.
Nevertheless, some progress has been made. The exercise of construing reported business behaviour in terms of accepted theory has revealed much
1 Andrews, On Competition, pp. 73-80.
2 Andrews, op. cit., pp. 90-93.
3. K.J. Cohen & R. M. Cyert, Theory of the Firm (New Jersey: Prentice-Hall, 1965), Chapter 3.
4. A. Silberston, “Surveys of Applied Economics: Price Behaviour of Firms,” Economic Journal, September, 1970. Professor Andrews’ death this year has deprived the profession of a widely-underrated, because misunderstood, economist.
more clearly than before the level of abstraction involved in that theory. One result is that micro-economists now have a somewhat better appreciation of the nature of their subject. Another is that the partial withdrawal of pretensions to describe the processes of decision-making by the use of the theory of the firm has facilitated the emergence of a very different paradigm for that purpose.
The logical justification for a separate paradigm of organisational decision-making was clearly set out for any one to see in Coase’s article “The Nature of the Firm.”  This article was presented as a skilful and wholly satisfying resolution of a very awkward anomaly in the theory of the firm - its failure, until that time, to account for the existence of firms at all in a specialised exchange economy. In explaining the allocation of economic decision-making between the market and a directing authority by applying marginal analysis to the cost of each kind of decision-process, Coase significantly reinforced the marginalist paradigm. But in basing his argument on the premise that decision-making within firms was different from decisions in the market, he excluded any detailed study of decision-making within firms from the fields of application of that paradigm. The theory of the firm might still be used as a highly-abstract model for predicting the overall results of the decisions of individual firms; but since bringing a decision within a firm implied, by definition, a rejection of the market mechanism, it now had a very limited sufficiency as a working model of the decision-making process.
The failure to notice this obvious implication of Coase’s work has resulted in much unnecessary expenditure of ink, time and temper. But though it may be thought unfortunate, it is not at all surprising that the article should be interpreted solely in terms of the paradigm which it employed, and that a new paradigm of business behaviour should have been created with small help from economists. That paradigm emerged primarily from concern with two organisational problems. On the one hand there was the question of organisational relationships, which was attracting increasing attention (primarily in the United States) from some psychologists and sociologists. On the other hand there was the need (implied in Coase’s analysis) for selective attention to problems and for economy in the search for solutions, which long remained the pragmatic concern of accountants establishing management control systems.
At first quite distinct, gradually these two areas of inquiry began to overlap, as increasing attention was given to behavioural aspects of control systems, and the inter-relationships of management structure and manage-
1. R. H. Coase, “The Nature of the Firm,” Economica, N S 1937; reprinted in Readings in Price Theory, pp. 331-51.
ment perception were more deeply explored. The major credit for evolving a new paradigm of organisational decision-making must go to H. A. Simon; and perhaps Simon’s critical contribution was the introduction of the concepts of limited knowledge and bounded rationality into his explanation of organisational cohesion, which made the identification of occasions for decision as crucial for him as for the designers of control systems. The new paradigm was introduced to economics by the work of Cyert and March.
Yet its impact has been very slight. To anyone accepting the argument hitherto, this should not be surprising. The failure to visualise economics explicitly as a systems study, and the dominance of market paradigms, conditioned economists to think of the firm as a basic element rather than as an economic system worthy of study in its own right. The widespread contempt exhibited by economists for accounting (the more scandalous for not being recognised as a scandal) prevented them from appreciating either the real difficulties or the practical importance of management control. Above all, the criteria employed in the existing paradigm were inevitably used in judging between it and the new; and on those criteria behavioural theory does rather badly. It has no answer to the questions of efficiency or stability as those questions are traditionally posed. It has no use for traditional basic concepts: optimisation has no usable meaning; economists’ heavy investment in calculus becomes redundant; equilibrium is not defined; and there are no general analytical solutions.
But the characteristics of one paradigm should not be used as the criteria by which a rival is judged. It is more helpful to compare the abstractions and the methods of analysis which are legitimised by each, the kinds of answer which each can give, and the questions which each permits to be asked. The critical distinction, which is a condition of all the others, is that between the definition of positions of rest and the specification of an ongoing process. (This is very like the distinction which Leijonhufvud regards as critical to an understanding of Keynes’ thought.)  As a consequence, instead of a defined goal, we have a defined origin. Thus, for example, a firm’s history and financial position become elements of the analysis, whereas in micro-equilibrium theory they are quite properly excluded as irrelevant. (Silberston’s criticism of standard theories of the firm on this score is misplaced.) 
Such a shift of focus, from destination to origin, has been a central feature of some major paradigm changes in other fields. It was, indeed, precisely such a shift, in the study of falling bodies, which gave rise to the concept of
1. Axel Leijonhufvud, Keynes and the Classics (London: Institute of Economic Affairs, 1969), p. 29.
2. Silberston, op. cit., p. 525.
instantaneous, as distinct from average, speed,  and thus in due course led to the development of differential calculus, which the equivalent shift in the theory of the firm now threatens to dethrone. It was precisely such a shift in the study of evolution which made Darwin’s ideas so disturbing; and it is apparently this absence of finality which most disturbs some critics of behavioural theory - not surprisingly, because it leaves us exposed forever to the “mystery and doubt” from which, as Shackle observes, we seek protection in theory. 
But exposure brings greater freedom. A process with no definable end does not lend itself to optimisation techniques of analysis, and so there is no pressure to build only optimising models. Instead, therefore, of being confined to studying the response of a system to changes in its parameters, one can develop a model in which these parameters become variables, and which therefore may initiate the changes to which it later responds. There is no need for the system to be dominated by negative feedback, as must necessarily be assumed - albeit unconsciously - in equilibrium models: the “cobweb theorem,” for instance, so anomalous in traditional micro-theory, fits easily into this type of analysis.
Another gain of freedom is in the handling of uncertainty. It is now possible to admit that in our world uncertainty is often a euphemism for ignorance, which cannot often be adequately represented by the use of certainty equivalents. It is the unknown, rather than the uncertain, which leads to the behaviour that Cyert and March categorise as uncertainty-avoidance,  and to the emphasis on flexibility as an objective in corporate strategy.  It is the unknown, rather than the uncertain, which makes satisficing rational. Satisficing is not equivalent to what Baumol and Quant call “optimally imperfect decision-making,”  not because it is “constrained maximisation with only constraints and no maximisation,”  but because it is embedded in a paradigm in which optimality has no definable meaning. Vickers’ model of long-run profit-maximisation, for example, relies on a series of conceptual production, investment and financing plans, of a precision which is irrational (which does not mean non-optimal) within the assumptions of the behavioural paradigm. 
Where there is neither finality nor optimality, there can hardly be general determinate solutions. It is the abandonment of the search for such solutions
1. Kuhn, op. cit., pp. 123-4.
2. Shackle, op. cit., pp. 288-9.
3. Cyert and March, op. cit., pp. 118—20.
4. H. I. Ansoff, Corporate Strategy (New York: McGraw-Hill, 1965), Chapter 4.
5. “which requires that the marginal cost of additional information gathering or more refined calculation be equal to its marginal (expected) gross yield.” W. J. Baumol and R. E. Quant, “Rules of Thumb and Optimally Imperfect Decisions,” American Economic Review, March 1964, p. 23.
6. Ibid., p. 24.
7. D. Vickers, The Theory of the Firm: Production, Capital and Finance (New York: McGraw-Hill, 1968).
that permits the use of behavioural variables in the way which gives behavioural theory its name. A fully determinate solution requires the behaviour, at least of relevant aggregates, to be fully constrained by the system. But if constraints are obligatory, objectives are optional, and the dilemma of micro-equilibrium theory is to reconcile the element of choice in the assumptions with the absence of choice in the results. This dilemma is brilliantly resolved in the theory of perfect competition, which combines completely independent decisions into a fully-determined system. Although normally employed in the exposition, the assumption of profit maximisation is redundant in this theory, at least in the long-run version: the behavioural assumptions are almost irrelevant, as a wide range of plausible assumptions all lead to the same result. Every objective turns out to be a constraint. The theory of imperfect competition with normal profits shares this highly desirable attribute; thus as long as free entry can be assumed, the behaviour of firms cannot affect the long-run equilibrium solution, and is not therefore a sensible subject for research. Within these limits, pricing behaviour is irrelevant to price theory. This essential point is thoroughly obscured in Silberston’s survey - not least effectively in its title.
The introduction of elements of monopoly destroys this happy conjuncture, for, in the absence of a perfect capital market and effective shareholder control of management, monopoly profits represent an area of discretion. Profit-maximisation does now become a necessary assumption for the unique determination of price and output; but for precisely the same reason, it is not the inevitable assumption: Baumol  and Williamson  have proferred plausible alternatives. If product differentiation is also allowed, one has a conceptual framework with very few general properties, but potentially rich in highly-specific hypotheses: in short, what economists call an empty model.
It does not, however, follow that elements of monopoly are necessary to behavioural theory, as seems to be generally believed (even by Cyert and March).  There is no reason why behavioural theory should not be applied to a firm which is a determined profit-seeker in a highly-competitive industry; it is not another version of monopoly or oligopoly theory, but a different paradigm, embodying a much lower degree of abstraction. Let us take three of the features which are normally regarded as evidence of some degree of monopoly. First, no organisation which delegates decision-making can avoid multiple objectives; and even if its objective function is well-defined, to distribute its components among managers in such a way as to produce organisationally-optimal decisions is hardly conceivable. Second, the need to allocate responsibility for sub-objectives, together with partial ignorance, makes the definition of objectives in terms of target levels,
1 W. J. Baumol, Business Behaviour, Value and Growth (New York: Macmillan, 1959).
2. 0. E. Williamson, The Economics of Discretionary Behaviour: Managerial Objectives in a Theory of the Firm (Chicago: Markham Publishing Co., 1967).
3. E.g., Silberston, op. cit., p. 536.
which are more often derived from experience than from optimising procedures, a rational policy. Third, there are many items of “managed costs,” which, by definition, represent an area of discretion, but which also enter as arguments into the profit function in ways which are often very poorly understood. In an equilibrium model, expenditures on such items as advertising, research, management training and management information and control systems, would appear as elements of long-run cost, each with an appropriate pay-off (no doubt including a stochastic term); but if neither equilibrium nor pay-offs can be specified, then these costs are most plausibly treated as discretionary, even apparently slack, payments: they are certainly likely to be cut in a cash squeeze - which might be non-optimal behaviour, if optimal behaviour could be defined.
The purpose of the previous section has been to demonstrate how different is the behavioural paradigm from any of the micro-equilibrium paradigms discussed earlier. It was not intended to demonstrate its superiority - indeed an important part of the argument of this paper has been that it is hard to find criteria for judging between paradigms that are not products of the paradigms themselves: rationality for example, apparently so objective, is in fact very heavily paradigm-dependent. Indeed, observant readers will have noticed that, like Kuhn’s view of scientific progress, the development of the theory of the firm, as presented in this article, falls entirely within the behavioural paradigm: problemistic search is evoked by a disparity between aspiration and the apparent performance of existing theories, and neither equilibrium nor optimality have any part to play in explaining the course of events.
If the new paradigm were to replace the old, much would be lost. But if it were to be finally rejected by economists, perhaps even more would be lost. For there are many areas of interest and issues of public policy in which the new has the advantage - for example, in questions of efficiency in the popular sense, and in analysing the character and the timing of responses to new situations (such as the introduction of S.E.T.). Fortunately, this is not, as it has sometimes been presented, a conflict for the title of the theory of the firm. For the most part, these paradigms operate at different system levels: once the effort has been made to view both of them with equal bias, there is nothing but an excessive and unscientific regard for consistency to prevent both being used, either separately or together as convenient, until the emergence of a new crisis and the rise of a new challenger. Perhaps next time, given a rather better appreciation of what is happening, the process will be rather less wasteful of time and energy; though it can never be either easy or comfortable.
BRIAN J. LOASBY
University of Stirling.