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The Methodology of Positive Economics
/Milton Friedman

Milton Friedman

"The Methodology of Positive Economics"

In Essays In Positive Economics

(Chicago: Univ. of Chicago Press, 1966), pp. 3-16, 30-43.


The Methodology of Positive Economics*


In his admirable book on The Scope and Method of Political

Economy, John Neville Keynes distinguishes among "a positive

science . . . a body of systematized knowledge concerning what is; a

normative or regulative science ... a body of systematized knowledge

discussing criteria of what ought to be . . . ; an art ... a system of

rules for the attainment of a given end"; comments that "confusion

between them is common and has been the source of many

mischievous errors"; and urges the importance of "recognizing a

distinct positive science of political economy."1

This paper is concerned primarily with certain methodological

problems that arise in constructing the "distinct positive science"

Keynes called for - in particular, the problem how to decide whether

a suggested hypothesis or theory should be tentatively accepted as

part of the "body of systematized knowledge concerning what is." But

the confusion Keynes laments is still so rife and so much of a

hindrance to the recognition that economics can be, and in part is, a

positive science that it seems well to preface the main body of the

paper with a few remarks about the relation, between positive and

normative economics.



Confusion between positive and normative economics is to some

extent inevitable. The subject matter of economics is regarded by

almost everyone as vitally important to himself and within the range

of his own experience and competence; it is

* I have incorporated bodily in this article without special reference

most of my brief "Comment" in A Survey of Contemporary Economics,

Vol. II (B. F. Haley, ed.) (Chicago: Richard D. Irwin, Inc., 1952), pp.


I am indebted to Dorothy S. Brady, Arthur F. Burns, and George J.

Stigler for helpful comments and criticism.

1. (London: Macmillan 4 Co., 1891), pp. 34-35 and 46.



the source of continuous and extensive controversy and the occasion

for frequent legislation. Self-proclaimed "experts" speak with many

voices and can hardly all be regarded as disinterested; in any event,

on questions that matter so much, "expert" opinion could hardly be

accepted solely on faith even if the "experts" were nearly unanimous

and clearly disinterested.2

The conclusions of positive economics

seem to be, and are, immediately relevant to important normative

problems, to questions of what ought to be done and how any given

goal can be attained. Laymen and experts alike are inevitably

tempted to shape positive conclusions to fit strongly held normative

preconceptions and to reject positive conclusions if their normative,

implications - or what are said to be their normative implications -

are unpalatable.

Positive economics is in principle independent of any particular

ethical position or normative judgments. As Keynes says, it deals with

"what is," not with "what ought to be." Its task is to provide a system

of generalizations that can be used to make correct predictions about

the consequences of any change in circumstances. Its performance is

to be judged by the precision, scope, and conformity with experience

of the predictions it yields. In short, positive economics is, or can be,

an "objective" science, in precisely the same sense as any of the

physical sciences. Of course, the fact that economics deals with the

interrelations of human beings, and that the investigator is himself

part of the subject matter being investigated in a more intimate sense

than in the physical sciences, raises special difficulties in achieving

objectivity at the same time that it provides the social scientist with a

class of data not available to the physical

2. Social science or economics is by no means peculiar in this respect -

witness the importance of personal beliefs and of "home" remedies in

medicine wherever obviously convincing evidence for "expert" opinion is

lacking. The current prestige and acceptance of the views of physical

scientists in their fields of specialization - and,, all too often, in other

fields as well - derives, not from faith alone, but from the evidence of

their works, the success of their predictions, and the dramatic

achievements from applying, their results. When economics seemed to

provide such evidence of its worth, in Great Britain in the first half of the

nineteenth century, the prestige and acceptance of "scientific economics"

rivaled the current prestige of the physical sciences.


scientist. But neither the one nor the other is, in my view, a fundamental

distinction between the two groups of sciences.3

Normative economics and the art of economics, on the other hand,

cannot be independent of positive economics. Any policy conclusion

necessarily rests on a prediction about the consequences of doing one

thing rather than another, a prediction that must be based - implicitly

or explicitly - on positive economics. There is not, of course, a

one-to-one relation between policy conclusions and the conclusions

of positive economics; if there were, there would be no separate

normative science. Two individuals may agree on the consequences

of a particular piece of legislation. One may regard them as desirable

on balance and so favor the legislation; the other, as undesirable and

so oppose the legislation.

I venture the judgment, however, that currently in the Western

world, and especially in the United States, differences about

economic policy among disinterested citizens derive predominantly

from different predictions about the economic consequences of taking

action - differences that in principle can be eliminated by the

progress of positive economics - rather than from fundamental

differences in basic values, differences about which men can

ultimately only fight. An obvious and not unimportant example is

minimum-wage legislation. Underneath the welter of arguments

offered for and against such legislation there is an underlying

consensus on the objective of achieving a "living wage" for all, to use

the ambiguous phrase so common in such discussions. The difference

of opinion is largely grounded on an implicit or explicit difference in

predictions about the efficacy of this particular means in furthering

the agreed-on end. Proponents believe (predict) that legal minimum

wages diminish poverty by raising the wages of those receiving less

than the minimum wage as well as of some receiving more than the

3. The interaction between the observer and the process observed that is

so prominent a feature of the social sciences, besides its more obvious

parallel in the physical sciences, has a more subtle counterpart in the

indeterminacy principle arising out of the interaction between the process

of measurement and the phenomena being measured. And both have a

counterpart in pure logic in Godel's theorem, asserting the impossibility

of a comprehensive self-contained logic. It is an open question whether

all three can be regarded as different formulations of an even more

general principle.


minimum wage without any counterbalancing increase in the number

of people entirely unemployed or employed less advantageously than

they otherwise would be. Opponents believe (predict) that legal

minimum wages increase poverty by increasing the number of people

who are unemployed or employed less advantageously and that this

more than offsets any favorable effect on the wages of those who

remain employed. Agreement about the economic consequences of the

legislation might not produce complete agreement about its

desirability, for differences might still remain about its political or

social consequences; but, given agreement on objectives, it would

certainly go a long way toward producing consensus.

Closely related differences in positive analysis underlie divergent

views about the appropriate role and place of trade-unions and the

desirability of direct price and wage controls and of tariffs. Different

predictions about the importance of so-called "economies of scale"

account very largely for divergent views about the desirability or

necessity of detailed government regulation of industry and even of

socialism rather than private enterprise. And this list could be

extended indefinitely.4 Of course, my judgment that the major

differences about economic policy in the Western world are of this

kind is itself a "positive" statement to be accepted or rejected on the

basis of empirical evidence.

If this judgment is valid, it means that a consensus on "correct"

economic policy depends much less on the progress of normative

economics proper than, on the progress of a positive economics

yielding conclusions that are, and deserve to be, widely accepted. It

means also that a major reason for

4. One rather more complex example is stabilization policy.

Superficially, divergent views on this question seem to reflect differences

in objectives; but I believe that this impression is misleading and that at

bottom the different views reflect primarily different judgments about the

source of fluctuations in economic activity and the effect of alternative

countercyclical action. For one major positive consideration that accounts

for much of the divergence see "The Effects of a Full-Employment Policy

on Economic Stability: A Formal Analysis," infra, pp. 117-32. For a

summary of the present state of professional views on this question see

"The Problem of Economic Instability," a report of a subcommittee of the

Committee on Public Issues of the American Economic Association,

American Economic Review, XL (September, 1950), 501-38.


distinguishing positive. economics sharply from normative economics

is precisely the contribution that can thereby be made to

agreement about policy.


The ultimate goal of a positive science is the development of a

"theory" or, "hypothesis" that yields valid and meaningful (i.e., not

truistic) predictions about phenomena not yet observed. Such a theory

is, in general, a complex intermixture of two elements. In part, it is a

"language" designed to promote "systematic and organized methods

of reasoning."5 In part, it is a body of substantive hypotheses

designed to abstract essential features of complex reality.

Viewed as a language, theory has no substantive content; it is a set

of tautologies. Its function is to serve as a filing system for

organizing empirical material and facilitating our understanding of it;

and the criteria by which it is to be judged are those appropriate to a

filing system. Are, the categories clearly and precisely defined? Are

they exhaustive? Do we know where to file each individual, item, or

is there considerable ambiguity? Is the system of headings and

subheadings so designed that we can quickly find an item we want, or

must we hunt from place to place? Are the items we shall want to

consider jointly filed together? Does the filing system avoid elaborate


The answers to these questions depend partly on logical, partly on

factual, considerations. The canons 'of formal logic alone can show

whether a particular language is complete and consistent, that is,

whether propositions in the language are "right" or "wrong." Factual

evidence alone can show whether the categories of the "analytical

filing system" have a meaningful empirical counterpart, that is,

whether they are useful in analyzing a particular class of concrete

problems.6 The simple example of "supply" and "demand" illustrates

both this point and the

5. Final quoted phrase from Alfred Marshall, "The Present Position of

Economics" (1885), reprinted in Memorials of Alfred Marshall, ed. A. C.

Pigou (London: Macmillan & Co., 1925), p. 164. See also "The

Marshallian Demand Curve," infra, pp. 56-57, 90-91.

6. See 'Lange on Price Flexibility and Employment: A Methodological

Criticism," infra, pp. 282-89.


preceding list of analogical questions. Viewed as elements of the

language of economic theory, these are the two major categories into

which factors affecting the relative prices of products or factors of

production are classified. The usefulness of the dichotomy depends on

the "empirical generalization that an enumeration of the forces

affecting demand in any problem and of the forces affecting supply

will yield two lists that contain few items in common.7 Now this

generalization is valid for markets like the final market for a

consumer good. In such a market there is a clear and sharp distinction

between the economic units that can be regarded as demanding the

product and those that can be regarded as supplying it. There is

seldom much doubt whether a particular factor should be classified as

affecting supply, on the one hand, or demand, on the other; and there

is seldom much necessity for considering cross-effects

(cross-references) between the two categories. In these cases the

simple and even obvious step of filing the relevant factors under the

headings of "supply" and "demand" effects a great simplification of

the problem and is an effective safeguard against fallacies that,

otherwise tend to occur. But the generalization is not always valid.

For example, it is not valid for the day-to-day fluctuations of prices in

a primarily speculative market, Is a rumor of an increased

excess-profits tax, for example, to be regarded as a factor operating

primarily on today's supply of corporate equities in the stock market

or on today's demand for them? In similar fashion, almost every

factor can with about as much justification be classified under the

heading "supply" as under the heading "demand." These concepts can

still be used and may not be entirely pointless; they are still "right"

but clearly less useful than in the first example because they have no

meaningful empirical counterpart.

Viewed as a body of substantive hypotheses, theory is to be

judged by its predictive power for the class of phenomena which it is

intended to "explain." Only factual evidence can show whether it is

"right" or "wrong" or, better, tentatively "accepted" as valid or

"rejected." As I shall argue at greater length below, the only relevant

test of the validity of a hypothesis is

7. "The Marshallian Demand Curve," infra, p. 57.


comparison I of its predictions with experience. The hypothesis

is rejected if its predictions are contradicted ("frequently" or

more often than predictions from an alternative hypothesis);

it is accepted if its predictions are not contradicted; great

confidence is attached to it if it has survived many opportunities

for contradiction. Factual evidence can never "prove" a hypothesis;

it can only fail to disprove it, which is what we generally

mean when we say, somewhat inexactly, that the hypothesis has

been "confirmed" by experience.

To avoid confusion, it should perhaps be noted explicitly that the

"predictions" by which the validity of a hypothesis is tested need not

be about phenomena that have not yet occurred, that is, need not be

forecasts of future events; they may be about phenomena that have

occurred but observations on which have not yet been made or are

not known to the person making the prediction. For example, a

hypothesis may imply that such and such must have happened in

1906, given some other known circumstances. If a search of the

records reveals that such and such did happen, the prediction is

confirmed; if it reveals that such and such did not happen, the

prediction is contradicted.

The validity of a hypothesis in this sense is not by itself a

sufficient criterion for choosing among alternative hypotheses.

Observed facts are necessarily finite in number; possible hypotheses,

infinite. If there is one hypothesis that is consistent with the available

evidence, there are always an infinite number that are.8 For example,

suppose a specific excise tax on a particular commodity produces a

rise in price equal to the amount of the tax. This is consistent with

competitive conditions, a stable demand curve, and a horizontal and

stable supply curve. But it is also consistent with competitive

conditions and a positively or negatively sloping supply curve with

the required compensating shift in the demand curve or the supply

curve; with monopolistic conditions, constant marginal costs, and

stable demand curve, of the particular shape required to produce this

result; and so on indefinitely. Additional evidence with which the

8. The qualification is necessary because the "evidence" may be

internally contradictory, so there may be no hypothesis consistent with it.

See also "Lange on Price Flexibility and Employment," infra, pp.



hypothesis is to be consistent may rule out some of these possibilities;

it can never reduce them to a single possibility alone capable

of being consistent with the finite evidence. The choice among

alternative hypotheses equally consistent with the available evidence

must to some extent be arbitrary, though there is general agreement

that relevant considerations are suggested by the criteria "simplicity"

and "fruitfulness," themselves notions that defy completely objective

specification. A theory is "simpler" the less the initial knowledge

needed to make a prediction within a given field of phenomena; it is

more "fruitful" the more precise the resulting prediction, the wider

the area within which the theory yields predictions, and the more

additional lines for further research it suggests. Logical completeness

and consistency are relevant but play a subsidiary role; their function

is to assure that the hypothesis says what it is intended to say and

does so alike for all users-they play the same role here as checks for

arithmetical accuracy do in statistical computations.

Unfortunately, we can seldom test particular predictions in the

social sciences by experiments explicitly designed to eliminate what

are judged to be the most important disturbing influences. Generally,

we must rely on evidence cast up by the "experiments" that happen to

occur. The inability to conduct so-called "controlled experiments"

does not, in my view, reflect a basic difference between the social

and physical sciences both because it is not peculiar to the social

sciences - witness astronomy and because the distinction between a

controlled experiment and uncontrolled experience is at best one of

degree. No experiment can be completely controlled, and every

experience is partly controlled, in the sense that some disturbing

influences are relatively constant in the course of it.

Evidence cast up by experience is abundant and frequently as

conclusive as that from contrived experiments; thus the inability to

conduct experiments is not a fundamental obstacle to testing

hypotheses by the success of their predictions. But such evidence is

far more difficult to interpret. It is frequently complex and always

indirect and incomplete. Its collection is often arduous, and its

interpretation generally requires subtle


analysis and involved chains of reasoning, which seldom carry real

conviction. The denial to economics of the dramatic and direct

evidence of the "crucial" experiment does hinder the adequate testing

of hypotheses; but this is much less significant than the difficulty it

places in the way of achieving a reasonably prompt and wide

consensus on the conclusions justified by the available evidence. It

renders the weeding-out of unsuccessful hypotheses slow and

difficult. They are seldom downed for good and are always cropping

up again.

There is, of course, considerable variation in these respects.

Occasionally, experience casts up evidence that is about as direct,

dramatic, and convincing as any that could be provided by

controlled experiments. Perhaps the most obviously important

example is the evidence from inflation on the hypothesis that a

substantial increase in the quantity of money within a relatively

short period is accompanied by a substantial increase in prices.

Here the evidence is dramatic, and the chain of reasoning

required to interpret it is relatively short. Yet, despite numerous

instances of substantial rises in prices, their essentially one-to

one correspondence with substantial rises in the stock of money,

and, the wide variation in other circumstances that might appear

to be relevant, each new experience of inflation brings forth

vigorous contentions, and not only by the lay public, that the

rise in the stock of money is either an incidental effect of a rise

in prices produced by other factors or a purely fortuitous and

unnecessary concomitant of the price rise.

One effect of the difficulty of testing substantive economic

hypotheses has been to foster a retreat into purely formal or

tautological analysis.9 As already, noted, tautologies have an

extremely important place in economics and other sciences as a

specialized language or "analytical filing system." Beyond this,

formal logic and mathematics, which are both tautologies, are

essential aids in checking the correctness of reasoning, discovering

the implications of hypotheses, and determining whether supposedly

different hypotheses may not really be equivalent or wherein the

differences lie..

But economic theory must be more than a structure of tautologies

9. See "Lange on Price Flexibility and Employment," infra, passim.

12 Essays in Positive Economics

if it is to be able to predict and not merely describe the consequences

of action; if it is to be something different from disguised

mathematics.10 And the usefulness of the tautologies themselves

ultimately depends, as noted above, on the acceptability of the

substantive hypotheses that suggest the particular categories into

which they organize the refractory empirical phenomena.

A more serious effect of the difficulty of testing economic

hypotheses by their predictions is to foster misunderstanding of the

role of empirical evidence in theoretical work. Empirical evidence is

vital at two different, though closely related, stages: in constructing

hypotheses and in testing their validity. Full and comprehensive

evidence on the phenomena to be generalized or "explained" by a

hypothesis, besides its obvious value in suggesting new hypotheses,

is needed to assure that a hypothesis explains what it sets out to

explain - that its implications for such phenomena are not

contradicted in advance by experience that has already been

observed.11 Given that the hypothesis is

10. See also Milton Friedman and L. J. Savage, "The Expected-Utility

Hypothesis and the Measurability of Utility," Journal of Political

Economy, LX (December, 1952), 463-74, esp. pp. 465-67.

11. In recent years some economists, particularly a group connected

with the Cowles Commission for Research in Economics at the University

of Chicago, have placed great emphasis on a division of this step of

selecting a hypothesis consistent with known evidence into two substeps:

first, the selection of a class of admissible hypotheses from all possible

hypotheses (the choice of a "Model" in their terminology) ; second, the

selection, of one hypothesis from this class (the choice of a "structure").

This subdivision may be heuristically valuable in some kinds of work,

particularly in promoting a systematic use of available statistical evidence

and theory. From a methodological point of view, however, it'is an

entirely arbitrary subdivision of the process of deciding on a particular

hypothesis that is on a par with many other subdivisions that may be

convenient for one purpose or another or that may suit the psychological

needs of particular investigators.

One consequence of this particular subdivision has been to give rise to

the so-called "identification" problem. As noted above, if one hypothesis

is consistent with available evidence, an infinite number are. But, while

this is true for the class of hypotheses as a whole, it may not be true of the

subclass obtained in the first of the above two steps-the "model." It may be

that the evidence to be used to select the final hypothesis from the subclass

can be consistent with at most one hypothesis in it, in which case the

"model" is said to be "identified"; otherwise it is said to be "unidentified."

As is clear from this way of describing the concept of "identification," it is

essentially a special case of the more general


consistent with the evidence at hand, its further testing involves

deducing from it new facts capable of being observed but not

previously known and checking these deduced facts against additional

empirical evidence. For this test to be relevant, the deduced

facts must be about the class of phenomena the hypothesis is

designed to explain; and they must be well enough defined so that

observation can show them to be wrong.

The two stages of constructing hypotheses and testing their

validity are related in two different respects. In the first place, the

particular facts that enter at each stage are partly an accident of the

collection of data and the knowledge of the particular investigator.

The facts that serve as a test of the implications of a hypothesis

might equally well have been among the raw material used to

construct it, and conversely. In the second place, the process never

begins from scratch; the so-called "initial stage" itself always

involves comparison of the implications of an earlier set of

hypotheses with observation; the contradiction of these implications

is the stimulus to the construction of new

problem of selecting among the alternative hypotheses equally consistent

with the evidence-a problem that must be decided by some such arbitrary

principle as Occam's razor. The introduction of two substeps in selecting a

hypothesis' makes this problem arise at the two corresponding stages and

gives it a special cast. While the class of all hypotheses is always

unidentified, the subclass in a "model" need not be, so the problem arises

of conditions that a "model" must satisfy to be identified. However useful

the two substeps may be in some contexts, their introduction raises the

danger that different criteria will unwittingly be used in making the same

kind-of choice among alternative hypotheses at two different stages.

On the general methodological approach discussed in this footnote see

Tryvge Haavelmo, "The Probability Approach in Econometrics,"

Econometrica, Vol. XII (1944), Supplement; Jacob Marschak, "Economic

Structure, Path, Policy, and Prediction," American Economic Review,

XXXVII, (May, 1947), 81-84, and "Statistical Inference in Economics: An

Introduction," in T. C. Koopmans (ed.), Statistical Inference in Dynamic

Economic Models (New York: John Wiley & Sons, 1950); T. C,

Koopmans, "Statistical Estimation of Simultaneous Economic Relations,"

Journal of the American Statistical Association, XL (December, 1945),

448-66; Gershon Cooper, "The Role of Economic Theory in Econometric

Models," Journal of Farm Economics, XXX (February, 1948), 101-16. On

the identification problem see Koopmans, "Identification Problems in

Econometric Model Construction," Econometrica, XVII (April, 1949),

125-44; Leonid Hurwicz, "Generalization of the Concept of

Identification," in Koopmans (ed.), Statistical Inference in Dynamic

Economic Models.


hypotheses or revision of old ones. So the two methodologically distinct

stages are always proceeding jointly.

Misunderstanding about this apparently straightforward process

centers on the phrase "the class of phenomena the hypothesis is

designed to explain." The difficulty in the social sciences of getting

new evidence for this class of phenomena and of judging its

conformity with the implications of the hypothesis makes it tempting

to suppose that other, more readily available, evidence is equally

relevant to the validity of the hypothesis-to suppose that hypotheses

have not only "implications" but also "assumptions" and that the

conformity of these "assumptions" to "reality" is a test of the validity

of the hypothesis different from or additional to the test by

implications. This widely held view is fundamentally wrong and

productive of much mischief. Far from, providing an easier means

for sifting valid from invalid hypotheses, it only confuses the issue,

promotes misunderstanding about the significance of empirical

evidence for economic theory, produces a misdirection of much

intellectual effort devoted to the development of positive economics,

and impedes the attainment of consensus on tentative hypotheses in

positive economics.

In so far as a theory can be said to have "assumptions" at all, and in

so far as their "realism" can be judged independently of the validity of

predictions, the relation between the significance of a theory and the

"realism" of its "assumptions" is almost the opposite of that suggested by

the view under criticism. Truly important and significant hypotheses will

be found to have "assumptions" that are wildly inaccurate des criptive

representations of reality, and, in general, the more significant the

theory, the more unrealistic the assumptions (in this sense).12 The reason

is simple. A hypothesis is important if it "explains" much by little, that

is, if it abstracts the common and crucial elements from the mass of

complex and detailed circumstances surrounding the phenomena to be

explained and permits valid predictions on the basis of them alone. To be

important, therefore, a hypothesis must be des criptively false in its

assumptions; it

12. The converse of the proposition does not- of course hold:

assumptions that are unrealistic (in this sense) do not guarantee a

significant theory.


takes account of, and accounts for, none of the many other attendant

circumstances, since its very success shows them to be irrelevant for

the phenomena to be explained.

To put this point less paradoxically, the relevant question to ask

about the "assumptions" of a theory is not whether they are

des criptively "realistic," for they never are, but whether they are

sufficiently good approximations for the purpose in hand. And this

question can be answered only by seeing whether the theory works,

which means whether it yields sufficiently accurate predictions. The

two supposedly independent tests thus reduce to one test.

The theory of monopolistic and imperfect competition is one

example of the neglect in economic theory of these propositions. The

development of this analysis was explicitly motivated, and its wide

acceptance and approval largely explained, by the belief that the

assumptions of "perfect competition" or, "perfect monopoly" said to

underlie neoclassical economic theory are a false image of reality.

And this belief was itself based almost entirely on the directly

perceived des criptive inaccuracy of the assumptions rather than on

any recognized contradiction of predictions derived from neoclassical

economic theory. The lengthy discussion on marginal analysis in the

American Economic Review some years ago is an even clearer,

though much less important, example. The articles on both sides of

the controversy largely neglect what seems to me clearly the main

issue - the conformity to experience of the implications of, the

marginal analysis - and concentrate on the largely irrelevant question

whether businessmen do or do not in fact reach their decisions by

consulting schedules, or curves, or multivariable functions showing

marginal cost and marginal revenue.13 Perhaps these

13. See R. A. Lester, "Shortcomings of Marginal Analysis for

Wage-Employment Problems," American Economic Review, XXXVI

(March, 1946), 62-82; Fritz Machlup, "Marginal Analysis and Empirical

Research," American Economic Review, XXXVI (September, 1946),

519-54; R. A. Lester, "Marginalism, Minimum Wages, and Labor

Markets," American Economic Review, XXXVII (March, 1947), 135-48;

Fritz Machlup, "Rejoinder to an Antimarginalist," American Economic

Review, XXXVII (March, 1947), 148-54; G. J. Stigler, "Professor Lester

and the Marginalists," American Economic Review, XXXVII (March,

1947), 154-57; H. M. Oliver, Jr., "Marginal Theory and Business

Behavior," American Economic Review,, XXXVII (June, 1947), 375-83;

R. A. Gordon,


two examples, and the many others they readily suggest, will

serve to justify a more extensive discussion of the methodological

principles involved than might otherwise seem appropriate.

"Short-Period Price Determination in Theory and Practice," American

Economic Review, XXXVIII (June, 1948), 265-88.

It should be noted that, along with much material purportedly

bearing on the validity of the "assumptions" of marginal theory, Lester

does refer to evidence on the conformity of experience with the

implications of the theory, citing the reactions of employment in

Germany to the Papen plan and in the United States to changes in

minimum-wage legislation as examples of lack of conformity.

However, Stigler's brief comment is the only one of the other papers

that refers to this evidence. It should also be noted that Machlup's

thorough and careful exposition of the logical structure and meaning

of marginal analysis is called for by the misunderstandings on this

score that mar Lester's paper and almost conceal the evidence he

presents that is relevant to the key issue he raises. But, in Machlup's

emphasis on the logical structure, he comes perilously close to presenting

the theory as a pure tautology, though it is evident at a number

of points that he is aware of this danger and anxious to avoid it. The

papers by Oliver and Gordon are the most extreme in the exclusive

concentration on the conformity of the behavior of businessmen with

the "assumptions" of the theory.



The abstract methodological issues we have been discussing have

a direct bearing on the perennial criticism of "orthodox" economic

theory as "unrealistic" as well as on the attempts that have been

made to reformulate theory to meet this charge. Economics is a

"dismal" science because it assumes man to be selfish and

money-grubbing, "a lightning calculator of pleasures and pains, who

oscillates like a homogeneous globule of desire of happiness under

the impulse of stimuli that shift him about the area, but leave him

intact"20; it rests on outmoded psychology and must be reconstructed

in line with each new development in psychology; it assumes men, or

at least businessmen, to be "in a continuous state of 'alert,' ready to

change prices and/or pricing rules whenever their sensitive intuitions

. . . detect a change in demand and supply conditions";21 it

20. Thorstein Veblen, "Why Is Economics Not an Evolutionary

Science?" (1898), reprinted in The Place of Science in Modern

Civilization (New York, 1919), p. 73.

21. Oliver, op. cit, p. 381.


assumes markets to be perfect, competition to be pure, and

commodities, labor, and capital to be homogeneous.

As we have seen, criticism of this type is largely beside the point

unless supplemented by evidence that a hypothesis differing in one or

another of these respects from the theory being criticized yields

better predictions for as wide a range of phenomena. Yet most such

criticism is not so supplemented; it is based almost entirely on

supposedly directly perceived discrepancies between the

"assumptions" and the "real world." A particularly clear example is

furnished by the recent criticisms of the maximization-of-returns

hypothesis on the grounds that businessmen do not and indeed cannot

behave as the theory "assumes" they do. The evidence cited to

support this assertion is generally taken either from the answers

given by businessmen to questions about the factors affecting their

decisions - a procedure for testing economic theories that is about on

a par with testing theories of longevity by asking octogenarians how

they account for their long life - or from des criptive studies of the

decision-making activities of individual firms.22 Little if any evidence

is ever cited on the conformity of businessmen's actual market

behavior - what they do rather than what they say they do - with the

implications of the hypothesis being criticized, on the one hand, and

of an alternative hypothesis, on the other.

22. See H. D. Henderson, "The Significance of the Rate of Interest,"

Oxford Economic Papers, No. I (October, 1938), pp. 1-13; J. E. Meade

and P. W. S. Andrews, "Summary of Replies to Questions on Effects of

Interest Rates," Oxford Economic Papers, No. I (October, 1938), pp.

14-31; R. F. Harrod, "Price, and Cost in Entrepreneurs' Policy," Oxford

Economic Papers, No. 2 (May, 1939), pp. 1-11; and R. J. Hall and C. J.

Hitch, "Price Theory and Business Behavior," Oxford Economic Papers,

No. 2 (May, 1939), pp. 12-45; Lester, "Shortcomings of Marginal

Analysis for Wage-Employment Problems," op. cit.; Gordon, op. cit. See

Fritz Machlup, "Marginal Analysis and Empirical Research," op. cit.,

esp. Sec. II, for detailed criticisms of questionnaire methods.

I do not mean to imply that questionnaire studies of businessmen's or

others' motives or beliefs about the forces affecting their behavior are

useless for all purposes in economics. They may be extremely valuable in

suggesting leads to follow in accounting for divergencies between

predicted and observed results; that is, in constructing new hypotheses or

revising old ones. Whatever their suggestive value in this respect, they

seem to me almost entirely useless as a means. of testing the validity of

economic hypotheses. See my comment on Albert G. Hart's paper,

"Liquidity and Uncertainty," American Economic Review, XXXIX (May,

1949), 198-99.


A theory or its "assumptions" cannot possibly be thoroughly

"realistic" in the immediate des criptive sense so often assigned, to

this term. A completely "realistic" theory of the wheat market. would

have to include not only the conditions directly underlying the supply

and demand for wheat but also the kind of coins or credit instruments

used to make exchanges; the personal characteristics of

wheat-traders such as the color of each trader's hair and eyes, his

antecedents and education, the number of members of his family,

their characteristics, antecedents, and education, etc.; the kind of soil

on which the wheat was grown, its physical and chemical

characteristics, the weather prevailing during the growing season; the

personal characteristics of the farmers growing the wheat and of the

consumers who will ultimately use it; and so on indefinitely. Any

attempt to move very far in achieving this kind of "'realism" is certain

to render a theory utterly useless.

Of course, the notion of a completely realistic theory is in part a

straw man. No. critic of a theory would accept this logical extreme

as his objective; he would say that the "assumptions" of the theory

being criticized were "too" unrealistic and that his objective was a set

of assumptions that were "more" realistic though still not completely

and slavishly so. But so long as the test of "realism" is the directly

perceived des criptive accuracy of the "assumptions" - for example,

the observation that "businessmen do not appear to be either as

avaricious or as dynamic or as logical as marginal theory portrays


or that "it would be utterly impractical under present

conditions for the manager of a multi-process plant to attempt . . . to

work out and equate marginal costs and marginal revenues for each

productive factor"24 there is no basis for making such a distinction,

that is, for stopping short of the straw man depicted in the preceding

paragraph. What is the criterion by which to judge whether a

particular departure from realism is or is not acceptable? Why is it

more "unrealistic" in analyzing business behavior to neglect the

magnitude of businessmen's costs than the

23. Oliver, op. cit, p. 382.

24. Lester, "Shortcomings of Marginal Analysis for Wage-Employment

Problems," op. cit., P. 75.


color of their eyes? The obvious answer is because the first makes

more difference to business behavior than the second; but there is no

way of knowing that this is so simply by observing that businessmen

do have costs of different magnitudes and eyes of different color.

Clearly it can only be known by comparing the effect on the

discrepancy between actual and predicted behavior of taking the one

factor or the other into account. Even the most extreme proponents

of realistic assumptions are thus necessarily driven to reject their

own criterion and to accept the test by prediction when they classify

alternative assumptions as more or less realistic.25

The basic confusion between des criptive accuracy and analytical

relevance that underlies most criticisms of economic theory on the

grounds that its assumptions are unrealistic as well as the

plausibility of the views that lead to this confusion are both

strikingly illustrated by a seemingly innocuous remark in an article

on business-cycle theory that "economic phenomena are varied and

complex, so any comprehensive theory of the business cycle that

can apply closely to reality must be very complicated."26 A

fundamental hypothesis of science is that appearances are deceptive

and that there is a way of looking at or interpreting or, organizing

the evidence that will reveal superficially disconnected and diverse

phenomena to be manifestations of a more fundamental and

relatively simple structure. And the test of this hypothesis, as of any

other, is its fruits - a test that science has

25. E.g., Gordon's direct examination of the "assumptions" leads him to

formulate the alternative hypothesis generally favored by the critics of the

maximization-of-returns hypothesis as follows: "There is an irresistible

tendency to price on the basis of average total costs for some 'normal'

level of output. This is the yardstick, the short-cut, that businessmen and

accountants use, and their aim is more to earn satisfactory profits and

play safe than to maximize profits" (op. cit., p. 275). Yet he essentially

abandons this hypothesis, or converts it into a tautology, and in the

process implicitly accepts the test by prediction when he later remarks:

"Full cost and satisfactory profits may continue to be the objectives even

when total costs are shaded to meet competition or exceeded to take

advantage of a sellers' market" (ibid, p. 284). Where here is the

"irresistible tendency"? What kind of evidence could contradict this


26. Sidney S. Alexander, "Issues of Business Cycle Theory Raised by

Mr. Hicks," American Economic Review, XLI (December, 1951), 872.


so far met with dramatic success. If a class of "economic phenomena"

appears varied and complex, it is, we must suppose,

because we have no adequate theory to explain them. Known facts

cannot be set on one side; a theory to apply "closely to reality," on

the other. A theory is the way we perceive "facts," and we cannot

perceive "facts" without a theory. Any assertion that economic

phenomena are varied and complex denies the tentative state of

knowledge that alone makes scientific activity meaningful; it is in a

class with John Stuart Mill's justly ridiculed statement that "happily,

there is nothing in the laws of value which remains [1848] for the

present or any future writer to clear up; the theory of the subject is


The confusion between des criptive accuracy and analytical

relevance has led not only to criticisms of economic theory on

largely irrelevant grounds but also to misunderstanding of economic

theory and misdirection of efforts to repair supposed defects. "Ideal

types" in the abstract model developed by economic theorists have

been regarded as strictly des criptive categories intended to

correspond directly and fully to entities- in the real world

independently of the purpose for which the model is being used. The

obvious discrepancies have led to necessarily, unsuccesful attempts

to construct theories on the basis of categories intended to be fully

des criptive.

This tendency' is perhaps most clearly illustrated by the interpretation

given to the concepts of "perfect competition" and

"monopoly" and the development of the theory of "monopolistic" or

"imperfect competition." Marshall, it is said, assumed "perfect

competition"; perhaps there once was such a thing. But clearly there

is no longer, and we must therefore discard his theories. The reader

will search long and hard - and I predict unsuccessfully - to find in

Marshall any explicit assumption about perfect competition or any

assertion that in a des criptive sense the world is composed of

atomistic firms engaged in perfect competition. Rather, he will find

Marshall saying: "At one extreme are world markets in which

competition acts directly from all parts of the globe; and at the other

those secluded

27. Principles of Political Economy (Ashley ed.; Longmans, Green &

Co., 1929), p. 436.


markets in which all direct competition from afar is shut out, though

indirect and transmitted competition may make itself felt even in

these; and about midway between these extremes lie the great

majority of the markets which the economist and the business man

have to study."28 Marshall took the world as it is; he sought to

construct an "engine" to analyze it, not a photographic reproduction

of it.

In analyzing the world as it is, Marshall constructed the hypothesis

that, for many problems, firms could be grouped into "industries"

such that the similarities among the firms in each group were more

important than the differences among them. These are problems in

which the important element is that a group of firms is affected alike

by some stimulus - a common change in the demand for their

products, say, or in the supply of factors. But this will not do for all

problems: the important element for these ni~ be the differential

effect on particular firms.

The abstract model corresponding to this hypothesis contains two

"ideal" types of firms: atomistically competitive firms, grouped into

industries, and monopolistic firms. A firm is competitive if the

demand curve for its output is infinitely elastic with respect to its

own price for some price and all outputs, given the prices charged by

all other firms; it belongs to an "industry" defined as a group of firms

producing a single "product." A "product" is defined as a collection

of units that are perfect substitutes to purchasers So the elasticity of

demand for the output of one firm with respect to the price of another

firm in the same industry is infinite for some price and some outputs.

A firm is monopolistic if the demand curve for its output is not

infinitely elastic at some price for all outputs.29 If it is a monopolist,

the firm is the industry.30

As always, the hypothesis as a whole consists not only of this

abstract model and its ideal types but also of a set of rules, mostly

28. Principles, p. 329; see also pp. 35, 100, 341, 347, 375, 546.

29. This ideal type can be divided into two types: the oligopolistic firm,

if the demand curve for its output is infinitely elastic at some price for

some but not all outputs; the monopolistic firm proper, if the demand

curve is nowhere infinitely elastic (except possibly at an output of zero).

30. For the oligopolist of the preceding note an industry can be defined

as a group of firms producing the same product.


implicit and suggested by example, for identifying actual firms with

one or the other ideal type and for classifying firms into industries.

The ideal types are not intended to be des criptive; they are designed

to isolate the features that are crucial for a particular problem. Even

if we could estimate directly and accurately the demand curve for a

firm's product, we could not proceed immediately to classify the firm

as perfectly competitive or monopolistic according as the elasticity of

the demand curve is or is not infinite. No observed demand curve will

ever be precisely horizontal, so the estimated elasticity will always be

finite. The relevant question always is whether the elasticity is

"sufficiently" large to be regarded as infinite, but this is a question

that cannot be answered, once for all, simply in terms of the

numerical value of the elasticity itself, any more than we can say,

once for all, whether an air pressure of 15 pounds per square inch is

"sufficiently" close to zero to use the formula S = 1/2gt2 Similarly,

we cannot compute cross-elasticities of demand, and then classify

firms into industries according as there is a "substantial gap in the

cross-elasticities of demand." As

Marshall says, "The question where the lines of division between

different commodities [i.e., industries] should be drawn

must be settled by convenience of the particular discussion."31

Everything depends on the problem; there is no inconsistency in

regarding the same firm as if it were a perfect competitor for

one problem, and a monopolist for another, just as there is none

in regarding the same chalk mark as a Euclidean line for one

problem, a Euclidean surface for a second, and a Euclidean

solid for a third. The size of the elasticity and cross-elasticity of

demand, the number of firms producing physically similar products,

etc., are all relevant because they are or may be among the

variables used to define the correspondence between the ideal and

real entities in a particular problem and to specify the circumstances

under which the theory holds sufficiently well; but they

do not provide, once for all, a classification of firms as competitive or


An example may help to clarify this point. Suppose the problem is

to determine the effect on retail prices of cigarettes of an

31. Principles, p. 100.


increase, expected to be permanent, in the federal cigarette tax. I

venture to predict that broadly correct results will be obtained by

treating cigarette firms as if they were producing an identical

product and were in perfect competition. Of course, in such a case,

"some convention must be made as to the" number of Chesterfield

cigarettes "which are taken as equivalent" to a Marlborough.32

On the other hand, the hypothesis that cigarette firms would

behave as if they were perfectly competitive would have been a

false guide to their reactions to price control in World War II, and

this would doubtless have been recognized before the event. Costs

of the cigarette firms must have risen during the war. Under such

circumstances perfect competitors would have reduced the

quantity offered for sale at the previously existing price. But, at

that price, the wartime rise in the income of the public presumably

increased the quantity demanded. Under conditions of perfect

competition strict adherence to the legal price would therefore

imply not only a "shortage" in the sense that quantity demanded

exceeded quantity supplied but also an absolute decline in the

number of cigarettes produced. The facts contradict this particular

implication: there was reasonably good adherence to maximum

cigarette prices, yet the quantities produced increased

substantially. The common force of increased costs presumably

operated less strongly than the disruptive force of the desire by

each firm to keep its share of the market, to maintain the value

and prestige of its brand name, especially when the excess-profits

tax shifted a large share of the costs of this kind of advertising to

the government. For this problem the cigarette firms cannot be

treated as if they were perfect competitors.

Wheat farming is frequently taken to exemplify perfect competition.

Yet, while for some problems it is appropriate to treat

cigarette producers as if they comprised a perfectly competitive

industry, for some it is not appropriate to treat wheat producers as

if they did. For example, it may not be if the problem is the

differential in prices paid by local elevator operators for wheat.

Marshall's apparatus turned out to be most useful for

problems in which a group of firms is affected by common


32. Quoted parts from ibid.


and in which the firms can be treated as if they were perfect

competitors. This is the source of the misconception that Marshall

"assumed" perfect competition in some des criptive sense. It would be

highly desirable to have a more general theory than Marshall's, one

that would cover at the same time both those cases in which

differentiation of product or fewness of numbers makes an essential

difference and those in which it does not. Such a theory would enable

us to handle problems we now cannot and, in addition, facilitate

determination of the range of circumstances under which the simpler

theory can be regarded as a good enough approximation. To perform

this function, the more general theory must have content and

substance; it must have implications susceptible to empirical

contradiction and of substantive interest and importance.

The theory of imperfect or monopolistic competition developed by

Chamberlin and Robinson is an attempt to construct such a more

general theory.33 Unfortunately, it possesses none of the attributes

that would make it a truly useful general theory. Its contribution has

been limited largely to improving the exposition of the economics of

the individual firm and thereby the derivation of implications of the

Marshallian model, refining, Marshall's monopoly analysis, and

enriching the vocabulary, available for describing industrial


The deficiencies of the theory are revealed most clearly in its

treatment of, or inability to treat, problems involving groups of

firms-Marshallian "industries." So long as it is insisted that,

differentiation of product is essential - and it is the distinguishing

feature of the theory that it does insist on this point - the definition of

an industry in terms of firms producing an identical product cannot

be used. By that definition each firm is a separate industry. Definition

in terms of "close" substitutes or a "substantial" gap in

cross-elasticities evades the issue, introduces fuzziness and

undefinable terms into the abstract model where they have no place,

and serves only to make the theory analytically meaningless - "close"

and "substantial" are in the same category

33. E. H. Chamberlin, The Theory of Monopolistic Competition (6tb

e.d.; Cambridge: Harvard University. Press, 1950); Joan Robinson, The

Economics of Imperfect Competition (London: Macmillan & Co., 1933).


as a "small" air pressure.34

In one connection Chamberlin implicitly defines an industry as a

group of firms having identical cost and demand curves." But this, too,

is logically meaningless so " long as differentiation of product is, as

claimed, essential and not to be put aside. What does it mean to say

that the cost and demand curves of a firm producing bulldozers are

identical with those of a firm producing hairpins?36 And if it is

meaningless for bulldozers and hairpins, it is meaningless also for two

brands of toothpaste - so long as it is insisted that the difference

between the two brands is fundamentally important.

The theory of monopolistic competition offers no tools for the

analysis of an industry and so no stopping place between the firm at

one extreme and general equilibrium at the other.37 It is therefore

incompetent to contribute to the analysis of a host of important

problems: the one extreme is too narrow to be of great interest; the

other, too broad to permit meaningful generalizations.38


Economics as a positive science is a body of tentatively accepted

generalizations about economic phenomena that can be used to

predict the consequences of changes in circumstances.

34. See R. L. Bishop, "Elasticities, Cross-elasticities, and. Market

Relationships," American Economic Review, XLII (December, 1952),

779-803, for a recent attempt to construct a rigorous classification of

market relationships along these lines. Despite its ingenuity and

sophistication, the result seems to me thoroughly unsatisfactory. It rests

basically on certain numbers being 'classified as "large" or "small," yet

there is no discussion at all of how to decide whether a particular number

is "large" or "small," as of course there cannot be on a purely abstract


35. Op. cit., p. 82.

36. There always exists a transformation of quantities that will make

either the cost curves or the demand curves identical; this transformation

need not, however, be linear, in which case it will involve different-sized

units of one product at different levels of output. There does not

necessarily exist a transformation that will make both pairs of curves


37. See Robert Triffin, Monopolistic Competition and General

Equilibrium Theory (Cambridge: Harvard University Press, 1940), esp.

pp. 188-89.

38. For a detailed critique see George J. Stigler, "Monopolistic

Competition in Retrospect," in Five Lectures on Economic Problems

(London: Macmillan & Co., 1949), pp. 12-24.


Progress in expanding this body of generalizations, strengthening

our confidence in their validity, and improving the accuracy of the

predictions they yield is hindered not only by the limitations of

human ability that impede all search for knowledge but also by

obstacles that are especially important for the social sciences in

general and economics in particular, though by no means peculiar to

them. Familiarity with the subject matter of economics breeds

contempt for special knowledge about it. The importance of its

subject matter to everyday life and to major issues of public policy

impedes objectivity and promotes confusion between scientific

analysis and normative judgment. The necessity of relying on

uncontrolled experience rather than on controlled experiment makes

it difficult to produce dramatic and clear-cut evidence to justify the

acceptance of tentative hypotheses. Reliance on uncontrolled

experience does not affect the fundamental methodological principle

that a hypothesis can be tested only by the conformity of its

implications or predictions with observable phenomena; but it does

render the task of testing hypotheses more difficult and gives greater

scope for confusion about the methodological principles involved.

More than other scientists, social scientists need to be self-conscious

about their methodology.

One confusion that has been particularly rife and has done

much damage is confusion about the role of "assumptions" in

economic analysis. A meaningful scientific hypothesis or theory

typically asserts that certain forces are, and other forces are not,

important in understanding a particular class of phenomena.

It is frequently convenient to present such a hypothesis by

stating that the phenomena it is desired to predict behave in

the world of observation as if they occurred in a hypothetical and

highly simplified world containing only the forces that the

hypothesis asserts to be important. In general, there is more

than one way to formulate such a des cription - more than one

set of "assumptions" in terms of which the theory can be presented.

The choice among such alternative assumptions is made

on the grounds of the resulting economy, clarity, and precision

in presenting the hypothesis; their capacity to bring indirect

evidence to bear on the validity of the hypothesis by suggesting


some of its implications that can be readily checked with observation

or by bringing out its connection with other hypotheses dealing with

related phenomena; and similar considerations.

Such a theory cannot be tested by comparing its "assumptions"

directly with "reality,." Indeed, there is no meaningful way in which

this can be done. Complete "realism" is clearly unattainable, and the

question whether a theory is realistic "enough" can be settled only by

seeing whether it yields predictions that are good enough for the

purpose in hand or that are better than predictions from alternative

theories. Yet the belief that a theory can be tested by the realism of

its assumptions independently of the accuracy of its predictions is

widespread and the source of much of the perennial criticism of

economic theory as unrealistic. Such criticism is largely irrelevant,

and, in consequence, most attempts to reform economic theory that it

has stimulated have been unsuccessful.

The irrelevance of so much criticism of economic theory does not

of course imply that existing economic theory deserves any high

degree of confidence. These criticisms may miss the target yet there

may be a target for criticism. In a trivial sense, of course, there

obviously is. Any theory is necessarily provisional and subject to

change with the advance of knowledge. To go beyond this platitude, it

is necessary to be more specific about the content of "existing

economic theory" and to distinguish among its different branches;

some parts of economic theory clearly deserve more confidence than

others. A comprehensive evaluation of the present state of positive

economics, summary of the evidence bearing on its validity, and

assessment of the relative confidence that each part deserves is clearly

a task for a treatise or a set of treatises, if it be possible at all, not for

a brief paper on methodology.

About all that is possible here is the cursory expression of

personal view. Existing relative price theory, which is designed to

explain the allocation of resources among alternative ends and the

division of the product among the co-operating resources, and which

reached almost its present form in Marshall's Principles of

Economics, seems to me both extremely fruitful and deserving of

much confidence for the kind of economic system


that characterizes Western nations. Despite the appearance of

considerable controversy, this is true equally of existing static, monetary

theory, which is designed to explain the structural or secular level of

absolute prices, aggregate output, and other variables for the economy

as a whole and which has had a form of the quantity theory of money as

its basic core in all of its major variants from David Hume to the

Cambridge School to Irving Fisher to John Maynard Keynes. The

weakest and least satisfactory part of current economic theory seems to

me to be in the field of monetary dynamics, which is concerned with the

process of adaptation of the economy as a whole to changes in conditions

and so with short-period fluctuations in aggregate activity. In this

field we do not even have a theory that can appropriately be called "the"

existing theory of monetary dynamics.

Of course, even in relative price and static monetary theory there is

enormous room for extending the scope and improving the accuracy of

existing theory. In particular, undue emphasis on the des criptive realism

of "assumptions" has. contributed to neglect of the critical problem of

determining the limits of validity of the various hypotheses that together

constitute the existing economic theory in these areas. The abstract

models corresponding to these hypotheses have been elaborated in considerable

detail and greatly improved in rigor and precision. Des criptive

material on the characteristics of our economic system and its

operations have been amassed on an unprecedented scale, This is all to

the good. But, if we are to use effectively, these abstract models and

this des criptive material, we must have a comparable exploration of the

criteria for determining what abstract model it is best to use for

particular kinds of problems, what entities in the abstract model are to

be identified with what observable entities, and what features of the

problem or of the circumstances have the greatest effect on the accuracy

of the predictions yielded by a particular model or theory.

Progress in positive economics will require not only the testing and

elaboration of existing hypotheses but also the construction of new

hypotheses. On this problem there is little to say on a


formal level. The construction of hypotheses is a creative act of

inspiration, intuition, invention; its essence is the vision of something

new in familiar material. The process must be discussed in

psychological, not logical, categories; studied in autobiographies and

biographies, not treatises on scientific method; and promoted by maxim

and example, not syllogism or theorem.




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