と題したエントリ(原題は「How economics took a wrong turn post World War II and an alternative theoretical framework for economics」)でMostly Economicsが、Meir Kohnダートマス大教授がケイトー研究所のCato Journal秋号に掲載した論文「An Alternative Theoretical Framework for Economics」を紹介している。以下はその論文の冒頭。

As a profession, economics is thriving. The number of economists is large and growing. The volume of their output is exploding—more articles are published each year in a growing number of journals. As a science, however, economics is not doing so well. The questions addressed by all those articles seem to be getting smaller and smaller. And there seems to be little or no progress on the big questions of economics such as economic development and growth, economic fluctuations, and the proper role of government in the economy. Most of the articles published are econometric, and the results of many are of questionable quality.
These problems of economics are, however, far from unique. There has been much talk in recent years of a general crisis of science. Despite ever more resources devoted to scientific research, the pace of scientific progress has slowed markedly. And the problems with statistical work in economics are part of a much broader “replicability crisis” in statistical work in general.
A major underlying cause of the general crisis of science is bureaucratization. Since World War II, scientific research has increasingly become concentrated in universities, and universities have become increasingly bureaucratized. Academic advancement has come to depend on metrics such as the number of publications in leading journals and the number of citations. Judging the significance of work is rarely even attempted: “deans can’t read, but they can count.” Incentives matter, and these bureaucratic incentives promote low‐​risk, low‐​value research. Bureaucratization is the result, in turn, of two related developments—the increasing adoption by universities of the model of the German research university, and the growing role of government in funding scientific research.
While economics shares with science in general the underlying cause of its problems, there is a specific factor in economics that has exacerbated these problems significantly—namely, a major wrong turn in economic theory. I will begin by describing the nature of this wrong turn, and then consider why it has been accepted so readily and why, indeed, it is a wrong turn. I will then discuss how economics has responded to the problems created by the wrong turn in theory and why that response has been inadequate. I will argue that the only real solution is to adopt a different theoretical framework. I will then describe, very briefly, a theory I have been developing and explain why this offers a better theoretical framework for economics as a whole. I will conclude by considering how economists might be persuaded to adopt this alternative framework.


The Wrong Turn in Economic Theory
In the period immediately after World War II, there was a transformation in the nature of economic theory—a change both in substance and in method. This transformation has its origins in the work of two great economists—Paul Samuelson and John Hicks.1 Samuelson wished to reformulate economic theory in the language of mathematics. He believed that doing so would promote greater clarity and precision, and he hoped that mathematization would lead to a formal unification of the whole of economic theory. While Samuelson’s goal was formal unification, Hicks’s goal was substantive unification. Hicks believed that much of economics could be understood in terms of the theory of value—the part of economics that seeks to explain the pattern of relative prices in an economy and the resulting allocation of resources.
Samuelson’s goals and Hicks’s proved highly complementary. The theory of value lends itself to mathematization. Hence, reducing economics to value theory offered a promising route to a more general mathematization of economics. The resulting mathematical model of value theory rapidly came to dominate economic theory. Indeed, for most economists, it became economic theory; this is the theory taught in today’s economics textbooks. I will refer to it in what follows as “the conventional theory.”2
The conventional theory came to dominate so quickly and so easily, because it met the needs of bureaucratic science. Mathematical modeling is technically difficult, but easy to grade. Moreover, it requires little or no acquaintance with actual economies—speeding up the production of publishable articles.3
However, these so‐​called advantages of the conventional theory come at a cost. Conventional theory constitutes a major narrowing of economic theory—in terms both of subject matter and of method. Before the Hicks‐​Samuelson revolution, the theory of value had been only one part of economics—certainly an important part, but still only a part. Other substantive areas included money and economic fluctuations, economic growth and development, economic institutions, and economic history.4 It turned out that these areas of economics, and others, could not be understood purely in terms of the theory of value and that, for them, mathematical modeling was not a fruitful theoretical method. This narrowing of economic theory has been a major reason for the lack of progress on the big questions of economics, since most of the big questions lie precisely in those areas in which conventional theory offers limited insight.


Responses to the Limitations of Conventional Theory
Economists have responded to the limitations of conventional theory in different ways. One way is denial: the areas of economics not amenable to the application of conventional economic theory are considered uninteresting.5
Some economists, however, have persisted in finding such areas interesting, and they have tried to develop particular theories, outside the conventional theory, appropriate to each area. Examples include the new institutional economics, transactions cost economics, public choice theory, and Austrian economics.6 Such attempts to go beyond conventional theory have been handicapped, however, by the lack of an overall theoretical framework into which they all fit. This limits the development of each by confining it to its own ghetto, outside the mainstream. To escape such ghettoes, some economists have attempted to fit their special theories into the Procrustean bed of conventional theory, with universally poor results.7
Yet other economists—in fact, most economists—have responded to the limitations of conventional theory by turning away from “theory” altogether, embracing instead a largely atheoretical applied econometrics.8 Work of this kind, like mathematical modeling, has the advantage of meeting the needs of bureaucratic science: it is technically challenging and, being atheoretical, can largely avoid the issue of whether it is important.9 However, avoiding that issue has allowed some econometric research to degenerate into “freakonomics”—the application of econometric methods to issues of questionable value in terms of advancing economics as a science.10
Moreover, it is increasingly recognized—and not only in economics—that good statistical work is impossible without an appropriate theoretical framework (see Pearl 2018; Henrich and Muthukrishna 2019). Only in the context of such a framework is it possible to judge whether an empirical question is important or not. And only in the light of theory is it possible to judge whether a statistical result is confirmatory or surprising. This matters, because surprising results are in greater need of further confirmation.11 Indeed, the atheoretical nature of much statistical work has been a major contributor to the replicability crisis.
These different responses to the limitations of conventional theory have therefore been, at best, only partly successful. What is really needed is a better theoretical framework. As it happens, I have one to offer! I did not set out to develop such a framework. I stumbled on it inadvertently.
従来理論の限界への以上の様々な対応は、従って、良くても部分的に成功したに過ぎない。真に必要とされているのは、より良い理論的枠組みである。そして私はたまたまそうした枠組みを持っている! 私はそうした枠組みを敢えて構築したわけではなく、意図せずして行き当たったのである。


How I Discovered an Alternative Theoretical Framework
I was trained as a mathematical theorist. However, from the beginning, I was very aware of the limitations of conventional theory, and I believed the answer lay in producing better models.12 But after many years of attempting to produce such models, I came to realize that better models are not the solution: however good my models were, they provided very little insight into how real‐​world economies worked.
Then, by chance, I discovered a completely different approach to theorizing. At the time, I was writing a textbook on financial intermediaries and markets, and I read some financial history as background. I found, however, that financial history offered much more than this: it offered more insight than any amount of mathematical modeling into why different financial institutions existed and what they did. So I switched from mathematical modeling to deriving theory from the observation of actual economies—in effect, a switch from Plato to Aristotle (Herman 2013).
My new method of theorizing might be described as one of “patterns and stories.”13 The first step is to study and observe an economy, or part of an economy, and to search for patterns in the evidence (the evidence may be qualitative as well as quantitative). The economy in question can be a contemporary economy, but historical economies have some advantages: they offer a longer period of observation, greater variation, and relative simplicity of structure. Their greatest advantage, however, is that the evidence is readily available from the extensive work of economic historians. There is much less evidence available for contemporary economies: economics does not value or reward mere description.14
The next step is to think of stories that might explain the observed patterns. The theory emerges from these stories. The theory is verbal rather than mathematical, describing and explaining the patterns observed in the historical evidence. Nelson argues that such a theory is nonetheless very much an abstract body of reasoning: “Certain variables and relationships are treated as important, and others are ignored. There generally is explicit causal argument” (Nelson 1998: 500).15
I decided to apply the method of patterns and stories to a more systematic study of financial systems—going back to the beginning in early preindustrial Europe. It soon became clear, however, that the most interesting and important economic question about financial systems is why, and how, they matter. Seeking an answer to this question led to mission creep: my goal expanded into developing a general theory of economic progress, which, among other things, would explain the role of the financial system.
As the work progressed, I came to realize that my theory of economic progress offered an alternative theoretical framework for economics as a whole—a much better one than that provided by conventional theory. That is not to say that my theory explained everything, but rather that it provided a framework into which much of the work outside the conventional theory could fit quite comfortably.

この辺りの話は、10/24エントリで紹介したJ.W. Masonの新しい経済学とも通底しているようにも思われる。