I have refrained from intervening in this debate so far because, alas, my
reading in German economic history is far from up to date.  The citations by
Albert Ritschl were rather daunting, and I planned to devote some time later in
the month to bring myself up to speed.  But given the volume of new work, that
might be a utopian aspiration, and I have read and worked sufficiently in this
field to formulate some thoughts. After reading Susan Boettcher's contribution,
I think it useful to weigh in now.

What this debate should not produce is a Methodenstreit about the most fruitful
path for historical research. After all, fruitful for whom? As historians we
follow agendas and use approaches that appeal to our interests and maximize our
gifts, and this is the way it should be. Cultural history addresses different
questions from economic history. Cultural history ultimately poses questions of
"meaning" -- whether through texts, artifacts, or social praxis and beliefs.
Economic history was traditionally based on, and must still deal with issues of
quantity: how much, how many, how prevalent (a question that must always be
answered with a denominator as well as a numerator). That is not its only
agenda, as Ritschl points out; but was a fundamental component. The
practitioners of economic history came on strong in the late l960s, which was a
decade that in general believed "social science" could provide the key to
social change.

They rightly pointed out that non-economic historians often made implicitly
quantitative statements (e.g. "to a degree," "often," "Not an inconsiderable
number..." "partly," etc., etc., that were devoid of any serious empirical
foundation). We do need quantities to think about "importance." The quantities
cannot settle the issue of significance, but they provide some testimony. On
the other hand, economic historians often suggested that once the quantitative
estimates were made, interpretations of significance and meaning would thereby
follow as a matter of course. They do not and they cannot.

I love reading cultural history, but my own sympathies are with those who
believe that "importance" or "significance" entails a quantitative estimation.
It was a great achievement for Carlo Ginzburg to open up the idea world of
Menocchio the Miller, for Natalie Davis to unfold the meanings of marriage and
family from Martin Guerre, and for Robert Darnton to show us the seething world
of class and rebelliousness in The Great Cat Massacre. These stories have
enriched our sense of the mental and societal worlds they explored and have
revealed new dimensions of social complexity and shared mentalities. So, too,
does David Sabean's explorations of village beliefs and structures. But I still
would like to know what share of Italian common folk might have shared
Menocchio's cosmology or some approximation thereof. Was Menocchio "typical" --
whether one wishes to define that as one out of two, or one out of twenty, or
even one out a hundred -- or just a total eccentric? The cultural historian
would find this issue beside the point, and indeed it may be for him or her.
Granted, the Inquisition must have believed Mennochio's views were potentially
contagious. Still, the question of numbers gets under my skin. Economic history
entails the assertion that such questions, while tiresome for some historians,
seem important for others.

Of course, some effort to press both the inquiries of economic history and
cultural history simultaneously is often important, although I often distrust
calls for "synthesis," as efforts prematurely to settle controversy, or a type
of cookbook prose. Not always, of course. Jonathan Zatlin's discussion of money
and scarcity in the GDR deploys both approaches. I have studied enough of the
GDR's economic system to understand how laden it was with specific values and
assumptions about the socialist citizen. The studies of the German inflation
that Gerald Feldman organized, and in which I participated, were critical for
assessing the impact of that experience. What does it mean for a family to
discover that monetary assets it believed it had accumulated had become
worthless? Yes, of course, that entails cultural inquiries. But for years we
encountered such generalizations as "The German inflation destroyed the middle
class" or "The German inflation brought about the rise of Hitler." Was it not
finally necessary to try to calculate who lost, who gained and how much? That
involved paintstaking work. The point is that most historians are offering
crypto-economic statements and they have often not been adequately tested.

There will always be room for further revision, but think for the moment what
major generalizations often found in German histories have been undermined by
economic history research: (1) The Prussian Junkers totally dominated their
servile peasantry (and thereby helped to perpetuate a feudal political system).
William Hagen's important study, however, suggests that the Brandenburg
peasantry maintained a far more robust standard of living and village
organization than our older images suggested. (2) Similarly, the "great
depression" (or more precisely, agricultural price stagnation or deflation)
from
1873-1896 led to the refeudalization of modern Germany, helped forge the Rye
and Iron domination of politics, cemented a protectionist coalition, enhanced
Junker domination of Prussia, etc. But the Great Depression has had a tendency
to crumble under close examination, such that all cause and effect statements
need to be made with far more care. (3) Germany emerged as a heavy-industry
dominated economy, rapidly overtaking Britain, and dominating the continent.
But we know from Sombart, and have been reminded by Adam Tooze, that by far
most workers were employed in small production units and agriculture remained a
singificant activity. And Gary Herrigel's work demonstrates how important the
Saxon model of diverse and "lighter" industry remained for German economic
development. And just to summarize other findings that some ecnomic reasoning
and economic research have problematized in the last few decades: reparations
did not have to be a hopeless burden; the Autobahn construction program did not
pull Germany out of the world economic crisis; high unemployment persisted in
Germany way into the Wirtschaftswunder.

The point of these examples is not to suggest that economic history replace
other investigations, but that without continual refinement of the economic
narratives we cannot make satisfactory statements about broader political and
national developments. Someone has to be doing this work. Moreover, as Ritschl
implies, economic theory has an intimate connection with other social theory in
the German context, preeminently by virtue of Weber's research program. And as
Zatlin observes, Germany is a nation-state in which economic performance and
organization have constituted a central thread of institutional life.  Consider
just the history of parliamentary representation: it was the need to finance
Prussian railway development that finally led to the summoning of an
all-Prussian assembly before 1848; the precursor of Bismarck's Reichstag was
the Zollparlament; the institutions of the Bundesrepublik grew out of the
Wirtschaftsrat that sat from l947 on.

That said, I am uneasy about the claims about theory that have emerged, and
usually emerge, on both sides in this debate. It is usually better to know more
math than less, just like more languages rather than fewer, but useful economic
history can be carried out at different levels of theory. To understand the
foundations of microeconomices it is helpful to understand partial derivatives
and probably matrix algebra. Albrecht Ritschl's model of the interaction
between foreign credits and reparations under the Young Plan (_Deutschlands
Krise und Konjunktur_, pp. 207-219) may elegantly put into mathematic terms the
relationships, but most of us will depend upon his prose explanation, which
rests upon reading and interpreting balance of payments figures. His book at
least provisionally resolves a long and crucial debate -- with some concessions
to the arguments made by both sides -- on Germany's financial policies in the
Great Depression (with obviously immense implications for the collapse of
Weimar). And while it may be true that without his own sophisticated mathematic
economic training, he would not have so clearly envisaged and articulated the
alternatives, not everyone need recapitulate his learning. To provide some
analogies, I cannot parse a complex musical score, but I am prepared to follow
an argument about Ring motifs or atonality. I am not equipped to understand
gauge theory but can grasp an account of quarks and gluons. History is a
discipline, I think, that presumes its practitioners are prepared to
communicate with a generally learned, but not always specially trained public.
Otherwise how could we claim that history as such, aside from its sub-fields,
even exists as a discipline?

On the other hand, it isn't really useful to say that economic history is
invalidated because it rests upon a simplistic model of homo oeconomicus or
maximizing man. Economists -- and not just those who deal with consumption --
recognize that we follow different sorts of impulses. An economist and an
economic historian easily recognizes that we can look for love in all the wrong
places, such as Porsche showrooms. The assumption is rather a tautological
starting point for modelling complex behavior -- namely that behavior
(including altruistic behavior) under normal circumstances does aim at
maximizing or "satisficing" (which is sufficient in many game- theoretic
models) some form of utility; and from that premise one can construct quite
sophisticated views of what actiities people will pursue as workers, as
consumers, as entrepreneurial planners. As a methodological premise it can be
compared with the historian's working presupposition, namely that we can learn
a lot about the present by examining earlier events. This, too, is a
significant simplification but one we need for our craft.

So, do we need a new economic history of Germany? That's not really been the
question debated in these contributions. Insofar as we "need" any history, we
will benefit from new economic histories of Germany. And not just histories of
consumption or culture-cum- economics, but nitty-gritty analyses of investment
and innovation, work and its compensation, decision-making and institution
building, decisions for public spending, class solidarities, cooperation and
conflict, financial constraints, the provision of welfare, the decisions to
form families and to migrate, the efficiency of the Nazi wartime economy, etc.,
etc. Indeed we cannot avoid investigating these topics insofar as we try to
think about German history more generally. Increasingly, though, I think it
will be useful to investigate this economic history in comparative context. In
what respects was German industrial organization unique; in what respects did
it differ from or share traits with other European or Asian or American
industrial societies?

Let me conclude by responding directly to Susan Boettcher's questions, which
prodded me into finally trying to react to this debate. I don't think that
econometrics can be interpreted as a quantitative version of capitalist theory,
although I'm not sure what is meant by capitalist theory. Econometrics uses
statistical correlation and regressions to try to establish the relations
between variables ---e.g. levels of education and wages, technological
innovation and productivity. The Soviets published a lot of econometrics
textbooks, and indeed the development of input-output economics, which was
crucial to central planning, required the sorts of statistical analysis that
went into cliometrics later on. As for the Peasant War, it may be that issues
involving the welfare of peasant communities, their burdens, etc., has been
thoroughly studied, just as grain prices before the French Revolution, or price
inflation in sixteenth-century Spain have received a great deal of attention.
I'm not sure I'd send graduate students back to look at 1923 at this point or
to the profitability of railroads versus canals in England and America. Not
that new data may not emerge, but we do tire of questions and some questions do
receive answers that satisfy us for a generation or more. Again Ritschl on
Germany's balance of payments constraints, or Tooze on the Nazi economy, seem
to offer a level of research and sophisticated response that may let us turn
our attention elsewhere. Nonetheless, it is probable that critics will emerge
to challenge their models or causal explanations.
Diminishing returns to scale is a fundamental presupposition of economic
analysis -- although, admittedly, not always Sraffan and neo- Marxian analysis
-- and I believe it applies to scholarship as well as the economic world. But
to decide that one cannot stomach yet another study of tithes in Swabia is
hardly equivalent to deciding that a whole area of inquiry throughout history
has been exhausted.

How often have great physicists felt that all the significant discoveries had
been made! Moreover, even questions that seem resolved from one perspective can
be reopened from others. If economic history were a capitalist plot, we would
never have had all the histories that were prompted originally by dependency
theory or world-systems analysis. Of course, we should encourage economic
literacy -- that was precisely the argument made by Tooze and Ritschl. On the
other hand, there are trade-offs: to study the economic history of Egypt, it
will help to be able to model the global demand for cotton, but it will also be
useful to know Arabic.

Ars lunga, vita brevis -- and graduate school even more so. My own feeling is
that all the issues of German economic development will yield new insights when
placed into global-history perspectives...just as cultural history is being
transformed by post-colonial theory. All of us have our work cut out for
ourselves.

	Charles S. Maier
	Harvard University

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