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Economic History and Economics

Robert Solow

Economic History and Economics
Robert M. Solow
The American Economic Review, Vol. 75, No. 2, (May, 1985), pp. 328-331.

I have in the back of my mind a picture of
the sort of discipline economics ought to be-or at least the sort of discipline I wish it
were. If economics were practiced in that
way there would be nothing problematical
about its reciprocal relationship with economic
history. It would be pretty clear what
it is that economic theory offers to economic
history and what economic history offers to
economic theory. I will try to describe what I
mean below.

For better or worse, however, economics
has gone down a different path, not the one I
have in mind. One consequence, not the most
important one, but the one that matters for
this discussion, is that economic theory learns
nothing from economic history, and economic
history is as much corrupted as enriched
by economic theory. I will come to
that, too, later on.

You will notice that I am using strong
language. I am prepared to admit right away
that I may be dead wrong in my judgements.
But there is no point in pussyfooting. Bluntness
may lead to an interesting discussion.
After all, no one would remember the old
German Historical School if it were not for
the famous Methodenstreit. Actually, no one
remembers them anyway. (There must be a
lesson in that.)

To get right down to it, I suspect that the
attempt to construct economics as an axiomatically
based hard science is doomed to fail.
There are many partially overlapping reasons
for believing this; but since that is not the
topic under discussion today, I do not have
to lay them out in an orderly way. I hope the
following hodgepodge will convey what I
mean.

A modern economy is a very complicated
system. Since we cannot conduct controlled
experiments on its smaller parts, or even
observe them in isolation, the classical hard science
devices for discriminating between
competing hypotheses are closed to us. The
main alternative device is the statistical analysis
of historical time-series. But then another
difficulty arises. The competing hypotheses
are themselves complex and subtle. We know
before we start that all of them, or at least
many of them, are capable of fitting the data
in a gross sort of way. Then, in order to
make more refined distinctions, we need long
time-series observed under stationary conditions.

Unfortunately, however, economics is a
social science. It is subject to Damon
Runyon’s Law that nothing between human
beings is more than three to one. To express
the point more formally, much of what we
observe cannot be treated as the realization
of a stationary stochastic process without
straining credulity. Moreover, all narrowly
economic activity is embedded in a web of
social institutions, customs, beliefs, and attitudes.
Concrete outcomes are indubitably
affected by these background factors, some
of which change slowly and gradually, others
erratically. As soon as time-series get long
enough to offer hope of discriminating among
complex hypotheses, the likelihood that they
remain stationary dwindles away, and the
noise level gets correspondingly high. Under
these circumstances, a little cleverness and
persistence can get you almost any result you
want. I think that is why so few econometricians
have ever been forced by the facts to
abandon a firmly held belief. Indeed, some
of Fortune’s favourites have been known to
write scores of empirical articles without once
feeling obliged to report a result that contradicts
their prior prejudices.

If I am anywhere near right about this, the
interests of scientific economics would be
better served by a more modest approach.
There is enough for us to do without pretending
to a degree of completeness and precision which we cannot deliver. To my way of thinking, the true functions of analytical
economics are best described informally:
to organize our necessarily incomplete
perceptions about the economy, to see connections
that the untutored eye would miss,
to tell plausible-sometimes even convincing-causal stories with the help of a few central
principles, and to make rough quantitative
judgments about the consequences of economic
policy and other exogenous events. In
this scheme of things, the end product of
economic analysis is likely to be a collection
of models contingent on society’s circumstances-
on the historical context, you might
say-and not a single monolithic model for
all seasons.

I hope no one here will think that this
low-key view of the nature of analytical
economies is a license for loose thinking.
Logical rigor is just as important in this
scheme of things as it is in the more self-consciously
scientific one. The same goes for
econometric depth and sophistication, maybe
even more so. I mentioned "rough" quantitative
judgment a moment ago, but that was
only to suggest that the best attainable, in
macroeconomics anyway, is not likely to be
precise, if we are honest with ourselves and
others. It would be a useful principle that
economists should actually believe the empirical
assertions they make. That would require
more discipline than most of us now
exhibit, when many empirical papers seem
more like virtuoso finger exercises than anything
else. The case I am trying to make
concerns the scope and ambitions of economic
model building, not the intellectual
and technical standards of model building.

I claimed earlier that the natural relation
between economics and economic history
would be clear and straightforward if only
economics were practiced in the fashion I
have just sketched. Now I had better say
what I meant. If economists set themselves
the task of modelling particular contingent
social circumstances, with some sensitivity to
context, it seems to me that they would
provide exactly the interpretive help an economic
historian needs. That kind of model is
directly applicable in organizing a historical
narrative, the more so to the extent that the
economist is conscious of the fact that different
social contexts may call for different
background assumptions and therefore for
different models.

The other direction of influence, what economic
history offers to that kind of economic
theory, is more interesting. If the proper
choice of a model depends on the institutional
context-and it should-then economic
history performs the nice function of
widening the range of observation available
to the theorist. Economic theory can only
gain from being taught something about the
range of possibilities in human societies. Few
things should be more interesting to a civilized
economic theorist than the opportunity
to observe the interplay between-social
institutions and economic behavior over time
and place.

I am going to illustrate by referring to the
work of W. H. B. Court, not merely because
his book The Rise of the Midland Industries
was on A. P. Usher’s reading list when I took
his course in the late 1940’s. I choose Court
for no better reason than that I happened to
run across an obituary article about him in
the Proceedings of the British Academy for
1982. (Since Court died in 1971. Fate did
seem to be playing a hand.)
Here, for instance, is an excerpt from
Court’s volume on Coal in the U.K.’s official
history of World War 11.

Observers who found the conduct of
the mineworkers puzzling assumed that,
in the normal way, a man who finds
himself faced with the possibilities of
higher earnings will be prepared to put
out extra effort to obtain them. An
assumption about the conduct of an
individual is as a rule, however, also an
assumption of some sort about the
society in which he lives and of which
he is a member. The individual’s demand
for income, his views upon the
getting and spending of money, are
usually formed by the part of society
which he is most in touch with. For
most men the social code, whatever it
may be in their time and place, is
something which they accept as given
and take over with little demur or questioning.
Before one can assume that a
demand for additional income existed
on the coalfields and could easily translate
itself into extra work, one has to
ask whether the mining community had
those standards or those habits. If it
did not, and if it was unable to develop
them in a short time, then even a rapid
rise of wage rates might bring about no
appreciable change in the working
habits of the industry.

In his own methodological writing, Court
made the point explicitly that men "living as
they do in different societies. ..make their
decisions according to different schemes of
values and according to the habits and structures
of the society they find themselves living in." Therefore an economic historian
should be an "observer and re-creator of the
codes, loyalties and organizations which men
create and which are just as real to them as
physical conditions." Add to that a command
over two-stage least squares and you
have the lund of economic historian from
whom theorists have most to learn. if only
they are willing to try. I have naturally lit on
this passage about the labor market because
that is the branch of theory I happen to be
engaged in right now, but no doubt the
thought would apply equally well to consumer
spending or rivalry among firms. I
must promise myself, before I lecture again
on wage bargaining, to ask my students to
read the chapters on "The Wage Bargain"
and "The Concept of the Minimum" in
Court’s British Economic History. 1870-
2 ,
1914: Commentary and Documents. I wonder
what they will make of it.

So much for the normative. If you read the
same journals I do, you may have noticed
that modern economics has an ambition and
style rather different from those I have been
advocating. My impression is that the best
and brightest in the profession proceed as if
economics is the physics of society. There is
a single universally valid model of the world.
It only needs to be applied. You could drop
a modern economist from a time machine-a
helicopter, maybe, like the one that drops the
money-at any time, in any place, along
with his or her personal computer; he or she
could set up in business without even
bothering to ask what time and which place.
In a little whle, the up-to-date economist
will have maximized a familiar-looking present-
value integral, made a few familiar loglinear
approximations, and run the obligatory
familiar regression. The familiar
coefficients will be poorly determined, but
about one-twentieth of them will be significant
at the 5 percent level, and the other
nineteen do not have to be published. With a
little judicious selection here and there, it
will turn out that the data are just barely
consistent with your thesis adviser’s hypothesis
that money is neutral (or non-neutral, take
your choice) everywhere and always, modulo
an information asymmetry, any old information
asymmetry, don’t worry, you’ll think of
one.

All right, so I exaggerate. You will recognize
the kernel of truth. We are socialized to
the belief that there is one true model and
that it can be discovered or imposed if only
you will make the proper assumptions and
impute validity to econometric results that
are transparently lacking in power.

Of course there are holdouts against this
routine, bless their hearts.

As I inspect current work in economic
history, I have the sinking feeling that a lot
of it looks exactly like the lund of economic
analysis I have just finished caricaturing: the
same integrals, the same regressions, the same
substitution of t-ratios for thought. Apart
from anything else, it is no fun reading the
stuff any more. Far from offering the economic
theorist a widened range of perceptions,
this sort of economic history gives
back to the theorist the same routine gruel
that the economic theorist gives to the
historian. Why should I believe, when it is
applied to thin eighteenth-century data,
sometlng that carries no conviction when it
is done with more ample twentieth-century
data?

The situation reminds me of a story I once
heard told by an anthropologist who had
spent some months recording the myths and
legends of a group of Apache in New Mexico.
One night, just before she was scheduled to
end her field work and depart, the Indians
said to her: We have been telling you our
legends all these months-why don’t you tell
us one of yours? The anthropologist thought
fast and then responded brilliantly by telling
the Indians a version of the story of Beowulf.
Years later she picked up a copy of an
anthropological journal and found in the
table of contents an article entitled "On the
Occurrence of a Beowulf-like legend among
the such-and-such Apache." If economic history
turns into something that could be described
as "The Occurrence of an Overlapping-
Generations-like Legend among the
Seventeenth-Century Neapolitans," then we
are at the point where economics has nothing
to learn from economic history but the bad
habits it has taught to economic history.

Let me recapitulate. If the project of turning
economics into a hard science could succeed,
it would surely be worth doing. No
doubt some of us should keep trying. If it
did succeed, then there would be no difference
between economics and economic
history other than the source of data, no
more than there is a difference between the
study of astronomical events taking place
now and those that took place in the Middle
Ages. In this dispensation an economic
historian is merely an economist with a high
tolerance for dust or-what is rarer these
days-a working knowledge of a foreign language.

There are, however, some reasons for pessimism
about the project. Hard sciences
dealing with complex systems-but possibly
less complex than the U.S. economy-like
the hydrogen atom or the optic nerve seem
to succeed because they can isolate, they can
experiment, and they can make repeated observations
under controlled conditions. Other
sciences, like astronomy, succeed because
they can make long series of observations
under natural but essentially stationary conditions,
and because the forces being studied
are not swamped by noise. Neither of these
roads to success is open to economists.

In that case, we need a different approach.
The function of the economist in this approach
is still to make models and test them
as best one can, but the models are more
likely to be partial in scope and limited in
applicability. "Testing" will have to be less
mechanical and more opportunistic, encompassing
a broader collection of techniques.
One will have to recognize that the validity
of an economic model may depend on the
social context. What is here today may be
gone tomorrow, or, if not tomorrow, then in
ten or twenty years’ time. In this dispensation
there is a clear and productive division
of labor between the economist and the economic
historian. The economist is concerned
with making and testing models of the economic
world as it now is, or as we think it is.
The economic historian can ask whether this
or that story rings true when applied in
earlier times or other places, and, if not, why
not. So the economic historian can use the
tools provided by the economist but will
need, in addition, the ability to imagine how
things might have been before they became
as they now are. These are the sensitivities
Court spoke of in the passage quoted
above. I take it, naively perhaps, that they
represent the comparative advantage of the
historian.

In return, economic history can offer the
economist a sense of the variety and flexibility
of social arrangements and thus, in particular,
a shot at understanding a little better
the interaction of economic behavior and
other social institutions. That strikes me as a
meaningful division of labor. It was once
suggested-by my kind of economist-that
the division of labor is limited by the extent
of the market. Perhaps what I have just been
doing can be thought of as marketing.

 
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