------ EH.NET BOOK REVIEW ------
Title: The Methodology of Positive Economics: Reflections on the Milton
Friedman Legacy
Published by EH.NET (November 2010)
Uskali Mäki, editor, /The Methodology of Positive Economics: Reflections on
the Milton Friedman Legacy./ Cambridge: Cambridge University Press, 2009.
xviii + 363 pp. $48 (paperback), ISBN: 978-0-521-68686-0.
Reviewed for EH.Net by Julian Reiss, Department of Philosophy, Erasmus
University.
Friedman’s 1953 essay, “The Methodology of Positive Economics,” is
undoubtedly one of the -- or perhaps /the/ -- most influential and most
widely and hotly debated papers on economic methodology. What economic
methodologist wouldn’t dream of having more than 2,500 citations in Google
Scholar for writing “the only essay on methodology that a large number,
perhaps majority, of economists have ever read” (Hausman 1992, 162)?
At the same time the essay appears somewhat difficult to interpret and, to
the extent that it has been interpreted, controversial. Indeed, many
different methodological perspectives have been read into it. According to
one interpreter, the essay “provides ingredients for a number of doctrines,
such as fictionalism, instrumentalism, positivism, falsificationism,
pragmatism, conventionalism, social constructivism, and realism” (Mäki
2003, 504) and “What the reader is served is an /F-mix/, a mixture of
ingredients many of which are ambiguous and some of which are hard to
reconcile with one another” (Mäki, 90; all undated page references are to
the volume under review); according to another, “One can find in it echoes,
and sometimes much more than echoes, of Popper, Kuhn, Quine, Toulmin, Laudan,
and even Feyerabend” (Blaug, 351). But this apparent confusion doesn’t
stop commentators taking a firm view on its worth: methodologists and
philosophers have generally taken a very critical stance whereas the majority
of practicing economists seems to endorse its conclusions, whatever they are
taken to be (Hands 2001, 57).
It should be no surprise, then, that more than half a century after its
publication, the essay still attracts an audience. The book under review is
the outcome of a 2003 conference held at Erasmus University Rotterdam to
celebrate the fiftieth anniversary of the essay’s publication. According to
its editor, the volume collects papers that “were commissioned from what
was close to the best possible team of scholars on the theme” (xviii).
It would be interesting to find out what this alleged “theme” is supposed
to be. The only thing that is clear after reading the book is that
Friedman’s 1953 methodological stance is not it. This is as startling for a
book that has the same title as Friedman’s essay as it is disappointing for
those, like me, who are interested in economic methodology and hope to learn
something new about methodological issues. Rather, the book comprises papers
on a wide variety of topics that are more or less loosely related to
Friedman’s essay, such as its genealogy, its historical context, whether it
caused the formalist revolution, whether it licensed the formalist
revolution, what type of methodology Friedman as a practicing economist
endorsed, and many more.
The absence of new material on the 1953 essay was particular disappointing to
me as a methodologist because (a) I don’t think the essay is quite as
obscure as some commentators make it appear (“Actually, it is at once
wonderfully ambiguous and incoherent” [Blaug, 351]); (b) in my view, the
position Friedman does defend in the essay has not made itself sufficiently
heard in recent times; and (c) the only chapter in the book that explicitly
deals with Friedman’s 1953 stance (Mäki, 90-116) makes an utterly
implausible case that the essay can be read (or “re-read” or
“re-written”; cf. the title of Mäki’s paper) as a statement of
realism. Let me go through these points in turn.
Ignoring labels for the time being, there can be no doubt about some of
Friedman’s 1953 methodological ideas. They can easily be summarized in two
prescriptions. The first prescription is that the aim of “positive”
economics -- along with the philosophical climate of his time and most
economists up to this day, Friedman believed in a strict dichotomy between a
realm of economic “facts” and another one of “values” -- is to devise
theories or hypotheses that successfully predict economic phenomena within
some domain of relevance (i.e., economists ought to conjecture such theories
or hypotheses). The second prescription is that economic theories or
hypotheses ought to be evaluated on the basis of the significance of their
assumptions and not their descriptive accuracy.
The qualifier “within some domain of relevance” of the first principle is
necessary to make the two principles coherent because an assumption implies
itself. If, for instance, some theory assumes that businessmen maximize
expected returns (Friedman, 21) whereas in fact they price at average cost
(22), the theory can be taken to predict that businessmen maximize expected
returns, which, being incorrect, would invalidate the theory. But once a
domain of relevance is identified (for Friedman in this case market prices
and quantities), assumptions and predictions can be distinguished.
The second principle has a positive and a negative part. To start with the
latter, Friedman thinks that the fact that an economic theory contains false
assumptions does not by itself speak against the theory. It is a
methodological truism that false theories can be predictively accurate --
Tycho’s geocentric system saved the phenomena no less than Copernicus’
heliocentric system for instance (McMullin 2009). To argue that a theory is
inadequate /because/ it contains false assumptions means therefore to commit
a methodological fallacy. However, that doesn’t mean that the assumptions
are irrelevant for evaluating a theory or that theories are to be evaluated
only with respect to their predictive success. Rather, and this is the
positive part of the second principle, assumptions should be
“significant,” by which Friedman means they should “explain much by
little” -- i.e., be simple and fruitful at the same time (Friedman, 10).
When he criticizes the theory of monopolistic competition for instance
(34ff.), Friedman never talks about its predictive success. He rejects it
because there is an alternative theory (neoclassical economic theory) that is
based on simpler and more fruitful assumptions. Thus, providing both theories
are equally “valid” (8f.) -- equally predictively successful -- the
neoclassical theory is preferable.
This is not the place for a full-fledged defense of Friedman’s methodology.
But since, as mentioned above, nearly all philosophical commentators have
been highly critical, let me suggest at least one reason why his position
might not be quite as unattractive as many philosophers and methodologists
have made it look.
The slogan “Essentially, all models are wrong, but some are useful” (Box
and Draper 1987, 424) has often been quoted, in economics and in many other
sciences. Many sciences are heavily model-driven, and economics is no
exception. Models are false by their very nature. Rather than sets of
statements, models are representations of their targets. All representations
must, on pain of utter uselessness, simplify, abstract, approximate, idealize
and what have you.
Those who think that truth is the aim of economics, or that understanding
economic phenomena is its aim and only true accounts provide genuine
understanding, have difficulty coming to terms with this fact. For not all
the ways in which a typical model distorts reality are equally harmless. In
rare cases, one can ignore an idealization because although it is literally
speaking false, it is still approximately true because the idealization makes
a negligible difference. But many models, especially in economics, are better
described in the following terms (Wimsatt 2007, 102, original emphasis): “A
model may give a /totally wrong-headed/ picture of nature. Not only are the
interactions wrong, but also a significant number of the entities and/or
their properties do not exist.”
I will say a little more below about the kinds of examples Friedman
discusses. What should be clear is that to the extent that such models play
an indispensable role in economics, as almost everyone agrees they do, those
who think that economics should aim for more than Friedman-style usefulness
have a lot of explaining to do.
Back to Friedman. As long as it is understood that the above two principles
form the core of Friedman’s methodology, it doesn’t matter a great deal
what label one attaches to it. Almost every label that has been proposed
captures some aspect correctly but is at the same time somewhat confusing
because of the connotations it brings with it. “Instrumentalism”
correctly captures the idea that lack of descriptive accuracy in a theory’s
assumptions isn’t a reason to reject it, but at the same time suggests that
“anything goes” as long as the theory predicts successfully, which is not
Friedman’s position. “Positivism” correctly captures Friedman’s
emphasis on prediction at the expense of explanation (he puts the latter term
in scare quotes whenever he uses it) but suggests an epistemic concern with
unobservables that Friedman does not have. “Pragmatism” correctly
captures Friedman’s aiming at practical usefulness rather than truth and
the central role user interest or purpose plays in his methodology, but it
suggests a denial of the fact-value dichotomy, in which Friedman was a firm
believer. “Fictionalism” correctly captures the idea that for a theory to
be useful it doesn’t have to be literally true but it ties Friedman’s
methodology to a little known and relatively obscure work of philosophy
(Vaihinger 1924; but see Fine 1993).
All the just mentioned philosophies are quite closely related, however, and
have one thing in common: they’re anti-realist. Realism is their common
enemy. In this light, it is all the more astonishing that the only chapter in
the book that is fully devoted to Friedman’s 1953 methodology tries to
present it as a statement of realism (Mäki, 90-116). How can its author, an
accomplished methodologist, make such a mistake?
Key to the misinterpretation may be Friedman’s continued use of a physics
example to illustrate methodological points. The law that predicts that the
distance travelled by a falling body is s = ½gt2 (Friedman, 16) is, when
applied to a compact ball dropped from the roof of a building, literally
speaking false because it assumes that the body falls in a vacuum. But since
air resistance makes a negligible difference /for this application/, the
hypothesis is useful nonetheless. Moreover, even when air resistance makes a
non-negligible difference, for instance, when the falling body is a feather
rather than a ball (17), the hypothesis is useful because it predicts the
contribution gravity makes to the fall. Gravity, like other forces in
mechanics, continues to contribute to outcomes even when its operation is
impeded by other causal factors such as air resistance.
But the mechanical example is exceptional and therefore misleading as an
illustration of Friedman’s methodological points. The test case for his
principles is the economic hypothesis that firms behave as if they were
rationally seeking to maximize their expected returns (21) -- after all, he
wrote the paper in response to the marginalist controversy (Backhouse,
235ff.). But “maximizing expected returns” isn’t analogous to “being
subject to f = ma” for at least three reasons. First, the maximizing
hypothesis doesn’t have the right form to be a hypothesis about a causal
factor that continues to contribute to an outcome in the presence of impeding
causal factors. A businessman whose pricing decisions are partly determined
by a fairness norm (say), does not maximize returns, not even approximately.
One either maximizes or one doesn’t, maximizing a little is like being a
little bit pregnant.
It is easy enough to come up with related hypotheses that have the right
form. It is not incoherent, for instance, to say that businessmen seek both
wealth and fairness. Economists then might focus on what happens when the
wealth motive operates unchecked by other motives. The problem with this
suggestion is that, by and large, what economic factors do depends on the
whole setting in which they are embedded. To talk about what gravity were to
do if it operated all on its own makes sense because situations can be
created in which gravity does operate all on its own -- or very nearly so. By
contrast, to ascribe a wealth motive to businessmen is nonsensical unless
certain kinds of institutional structure are presupposed. Indeed, applying
the term “businessman” presupposes such an institutional setting. In
turn, details of the structure in which any motive of action is embedded will
influence the behavior that is caused by the motive. Thus, unlike physical
forces, which have a stable contribution to outcomes independently of
context, what economic factors do tends to be more context-specific.
Therefore, what we learn about how certain motives -- such as seeking wealth
-- operate when other motives for action are absent, even if correct for that
situation, tends not to be very useful for predicting what happens in more
complex situations.
Third, Friedman thinks that actual businessmen use an average cost pricing
rule (22). Suppose he is right. This would mean that the assumption that they
maximize returns is not idealizing away other causal factors but rather
portraying a radically different factor, an “entity or property that does
not exist” in Wimsatt’s words, as being responsible for outcomes of
interest.
On all three counts, therefore, to assume that businessmen maximize returns
is to give a totally wrong-headed picture of society. No realist defense of
idealization I can think of can make sense of this part of Friedman’s
story. And this is the essential part of his story.
Putting aside the fact that there’s very little about the methodology of
Friedman 1953 in this book, and that what there is is highly implausible to
say the least, the remaining essays do contain some interesting and useful
material. Dan Hammond recounts the genesis of the essay and how it changed
from drafts into the published version in response to comments from other
economists such as George Stigler. Thomas Mayer tries to answer the question
of whether the essay caused the changing appearance of economics in the
second half of the twentieth century (the “formalist revolution”). Wade
Hands asks whether it /licensed/ the formalist revolution and in particular
who is right between Blaug and Hutchison, who have argued that it did, or
Mayer, who has argued that it didn’t. (Hands’ short answer is that Mayer
is right.) Melvin Reder assesses to what extent empirical evidence can bear
on the neoclassical theory of wage setting. David Teira and Jesús Zamora
argue that Friedman proposed his principle that the validity of economic
hypotheses is determined by their predictive success as a way to gain the
trust of public opinion regarding the claims established by the profession.
Roger Backhouse locates the essay in the context of the marginalist
controversy of the 1940s. Oliver Williamson writes about the theory of the
firm and that it badly needs (but as of lately, also makes) testable
empirical predictions. Jack Vromen provides a critical survey of selection
arguments in favor of the maximizing hypothesis. Chris Starmer contrasts the
explicit methodology of the 1953 essay with two “methodology in action”
pieces written by Friedman with Leonard Savage in 1948 and 1952. Kevin Hoover
inspects the implicit methodology of Friedman as a practicing economist and
identifies it as “causal realist.” Michel de Vroey asks whether there
really is a divide between “Marshallian” and “Walrasian” economics,
as Friedman claimed in a paper written in 1949 (though not in the 1953
paper). Mark Blaug looks at the debate over the essay after 50 years and
argues that “Friedman may have won some methodological battles” but
“lost the methodological war” (353) because, as he demonstrated in his
/Monetary History of the United States/ (Friedman and Schwartz 1963) Friedman
sought “thick evidence,” that is, a wide variety of different kinds of
mutually corroborating evidence, whereas most of the profession contends with
narrow or “thin” econometric evidence. A “Final Word” by Friedman
himself concludes the book.
If one understands the book as one on Friedman rather than the 1953 essay, it
is quite a pleasure to read.
References:
Box, George and Norman Draper (1987). /Empirical Model-Building and Response
Surfaces/. New York: John Wiley & Sons.
Fine, Arthur (1993). "Fictionalism." /Midwest Studies in Philosophy/ XVIII:
1-18.
Friedman, Milton. 1953. “The methodology of positive economics”
(‘Friedman 1953’). Reprinted in Uskali Mäki (ed). 2009. /The Methodology
of Positive Economics/, 3-42
Friedman, Milton and Anna Schwartz (1963). /A Monetary History of the United
States, 1867–1960/. Princeton, Princeton University Press.
Hands, D. Wade (2001). /Reflection without Rules: Economic Methodology and
Contemporary Science Theory/. Cambridge, Cambridge University Press.
Hausman, Daniel (1992). /The Inexact and Separate Science of Economics/.
Cambridge, Cambridge University Press.
Mäki, Uskali (2003). "The Methodology of Positive Economics (1953) Does Not
Give Us the Methodology of Positive Economics." /Journal of Economic
Methodology/ 10(4): 495-505.
McMullin, Ernan (2009). "Hypothesis in Early Modern Science." /The
Significance of the Hypothetical in the Natural Sciences/. M. Heidelberger
and G. Schiemann (ed.). Berlin, de Gruyter: 7-38.
Vaihinger, Hans (1924). /The Philosophy of 'As If': A System of the
Theoretical, Practical and Religious Fictions of Mankind/. London, Routledge
and Keagan Paul.
Wimsatt, William (2007). /Re-engineering Philosophy for Limited Beings:
Piecewise Approximations to Reality/. Cambridge (MA), Harvard University
Press.
Julian Reiss is associate professor in the faculty of philosophy at Erasmus
University Rotterdam. His research focuses on the philosophy of science, the
history and philosophy of economics, and philosophy of medicine. His latest
book is /Error in Economics: Towards a More Evidence-based Methodology/
(Routledge, 2008).
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Geographic Location: General, International, or Comparative, North America
Subject: History of Economic Thought; Methodology
Time: 20th Century: WWII and post-WWII
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