DUMB AND DUMBER IN MACROECONOMICS Robert M. Solow So

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DUMB AND DUMBER IN MACROECONOMICS
Robert M. Solow
So how did macroeconomics arrive at its current state? The answer might
provide a lead as to where it ought to go.
The original impulse to look for better or more explicit micro foundations was
probably reasonable. It overlooked the fact that macroeconomics as practiced by
Keynes and Pigou was full of informal microfoundations. (I mention Pigou to
disabuse everyone of the notion that this is some specifically Keynesian thing.)
Generalizations about aggregative consumption-saving patterns, investment patterns,
money-holding patterns were always rationalized by plausible statements about
individual--and, to some extent, market--behavior. But some formalization of the
connection was a good idea. What emerged was not a good idea. The preferred model
has a single representative consumer optimizing over infinite time with perfect
foresight or rational expectations, in an environment that realizes the resulting plans
more or less flawlessly through perfectly competitive forward-looking markets for
goods and labor, and perfectly flexible prices and wages.
How could anyone expect a sensible short-to-medium-run macroeconomics to
come out of that set-up? My impression is that this approach (which seems now to be
the mainstream, and certainly dominates the journals, if not the workaday world of
macroeconomics) has had no empirical success; but that is not the point here. I start
from the presumption that we want macroeconomics to account for the occasional
aggregative pathologies that beset modern capitalist economies, like recessions,
intervals of stagnation, inflation, "stagflation," not to mention negative pathologies
like unusually good times. A model that rules out pathologies by definition is unlikely
to help. It is always possible to claim that those "pathologies" are delusions, and the
economy is merely adjusting optimally to some exogenous shock. But why should
reasonable people accept this? During the past three years, unemployment has
increased by three million with real wages stagnant and productivity growing,
possibly abnormally fast. Capacity utilization has fallen by 10 percent, with trivial
inflation and some prices falling. Real business investment in equipment peaked in
the third quarter of 2000, fell by 20 percent to the first quarter of 2002, and has risen
by a scant five percent since then. Is this a stagnation pattern? Does it reflect largescale, perhaps irrational, overinvestment in the 1990s? Should it not be studied as
such? Why should anyone take it as the solution of an Euler equation? It would not
be hard to imagine a better path for the economy. Why should the burden of proof fall
on those who see an ordinary standard pathology here? The odd thing is to regard this
history as the working out of an other-worldly model.
What is needed for a better macroeconomics? My crude caricature of the
Ramsey-based model suggests some of the gross implausibilities that need to be
eliminated. The clearest candidate is the representative agent. Heterogeneity is the
essence of a modern economy. In real life we worry about the relations between
managers and shareowners, between banks and their borrowers, between workers and
employers, between venture capitalists and entrepreneurs, you name it. We worry
about those interfaces because they can and do go wrong, with likely macroeconomic
consequences. We know for a fact that heterogeneous agents have different and
sometimes conflicting goals, different information, different capacities to process it,
different expectations, different beliefs about how the economy works.
Representative-agent models exclude all this landscape, though it needs to be
abstracted and included in macro-models.
I also doubt that universal rational expectations provide a useful framework for
macroeconomics. One understands the appeal. Think of it this way: Herb Simon was
surely right about bounded rationality; no one would deny that most economic agents
are actually like that, and natural selection does not work fast enough to eliminate
them. Why did the notion of "satisficing" never catch on? I think it is because the
assumption of complete rationality tells the modeller what to do, whereas bounded
rationality only tells the modeller what not to do. That is not helpful. Something
similar is true about rational expectations. If there were a nice parametric family of
alternative ways to model expectations, it might catch on. Most of us would happily
go along with the notion of expectational equilibrium: if specific underlying
expectations generate an outcome in which those expectations are systematically and
non-trivially violated, that situation can not be an equilibrium. It is what happens then
that needs thought. The situations that agents need to anticipate need not even be
probabilistic, surely not stationary. The popular device used to be adaptive
expectations; that may have been inadequate. Maybe this is a case for the application
of psychological research (and sociological research as well, because the formation
of expectations is a social process). Maybe experiments can be designed.
Heterogeneity across agents and classes of agents is certainly important precisely
here. One would like a simple, definite way to proceed, if that is possible. A good
example of the sort of thing I mean is the way the Dixit-Stiglitz model made
monopolistic competition easy. (The trouble is that we are dealing with an
unobservable.)
Although I am going to take this back in a moment, it is certainly worthwhile
mentioning the problems connected with real and/or nominal wage and price
inflexibility and its sources in market structure, limitations of information, human
nature, the specialness of zero, etc. This is an old issue in economics, macro and
micro, and a lot of progress has been made in measuring and understanding it. Mere
sluggishness is part of the picture, and that is easily modelled, but there is surely more
that is less easily modelled. The devil finds work for idle hands to do, as you may
have noticed.
Now here is a peculiar thing. When I was in advanced middle age, I suddenly
woke up to the fact that my colleagues in macroeconomics, the ones I most admired,
thought that the fundamental problem of macro theory was to understand how
nominal events could have real consequences. This is just a way of stating some
puzzle or puzzles about the sources for sticky wages and prices. This struck me as
peculiar in two ways.
First of all, when I was even younger, nobody thought this was a puzzle. You
only had to look around you to stumble on a hundred different reasons why various
prices and factor prices should be much less than perfectly flexible. I once wrote,
archly I admit, that the world has its reasons for not being Walrasian. Of course I
soon realized that what macroeconomists wanted was a formal account of price
stickiness that would fit comfortably into rational, optimizing models. OK, that is a
harmless enough activity, especially if it is not taken too seriously. But price and
wage stickiness themselves are not a major intellectual puzzle unless you insist on
making them one.
The second peculiarity was that the path from nominal events to real
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consequences was not my idea of the fundamental problem of macro theory anyway.
All along, I had been thinking--and this may be a Keynesian inheritance, though I
doubt it because I may have picked it up from Gottfried Haberler's Prosperity and
Depression, where my generation learned about business-cycle theory before
"macroeconomics" had been invented--that the main problem was to understand why
real shocks that took the economy out of some satisfactory equilibrium led to such a
prolonged and sometimes unsatisfactory adjustment. These are medium-run problems-the capital stock moves--and there clearly are medium-run fluctuations in modern
industrial economies. (This is documented for the U.S. in a recent paper by Comin
and Gertler.)
Keynes claimed to have found the way to account for this: he thought he had
a theory of unemployment equilibrium. The reason adjustment took so long, or never
really happened, is that the depressed state was actually an equilibrium. Most of us
today think that Keynes failed in that effort; he lacked the tools. The exception was
the case of wage rigidity, but we knew that all along. In my youth, we thought that
macro-pathologies were disequilibrium phenomena, and then the puzzle was: why is
the process so slow?
This choice between equilibrium and disequilibrium thinking may be a false
choice. If I drop a ripe watermelon from this 15th-floor window, I suppose the whole
process from t0 to the mess on the sidewalk could be described as some sort of
dynamic equilibrium. But that may not be the most fruitful--sorry--way to describe
the falling-watermelon phenomenon.
So I would hope that macro theory could get back to focussing on the
adaptation-to-real-disturbance problem, without falling into the implausibilities of
real-business-cycle theory. (Even RBC theorists may fight their way out of that paper
bag.) The Ur-Problem may be: start in a situation of growth equilibrium (not
necessarily a steady state, but don't get me started on that one), and imagine a real
shock, perhaps a failure of real effective demand (!). What happens next? That may
be the story of the period from 2000 to now, the real shock having been massive
overinvestment in response to unrealistic profit expectations (accompanied by
accounting swindles, just to make Joe happy).
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