Economic history in the future will be shaped by economic history in the past, but it also needs to transcend that past. In particular, it needs to transcend the breakdown of the field's original interdisciplinary structure and its transformation into a subfield of economics. Most economists and historians today accept the stereotype that economics is about generalization and history is about understanding specific phenomena in the past. There is some validity to this stereotype, but I will argue that economic historians must operate somewhere in the middle of those extremes if they are truly to advance knowledge. Most research by economic historians trained as economists does not in fact produce universal generalizations and to treat it as such, rather than to acknowledge its context-specific character, is to mislead. At the same time, research in history risks degenerating into antiquarianism when scholars amass information about their specific topics without worrying about how their work might inform those who study other times and places, including the present. As a matter of actual practice, critical discussion in both disciplines tends to push scholars toward the middle of this range. Economists are continually forced to acknowledge the limits on their generalizations, and historians face relentless “so what?” questions. Nonetheless, I would argue, the ability of economic historians to function effectively on this middle terrain has long been hampered by a lack of interdisciplinary conversation.Footnote ¹

The lack of communication between economics and history is the product of two developments: the cliometric revolution in economic history; and the cultural turn in the historical profession more generally. The story of these developments is well known (see, for example, Williamson 1994; Lyons, Cain, and Williamson 2008; and Bonnell and Hunt 1999). I have written about them myself (Lamoreaux 1998, 2016 (forthcoming)) and do not intend to go over that material again here. Instead, I will simply use some examples from early cliometric scholarship to underscore my argument about the tendency of economic historians to move toward the middle. Cliometricians initially drew sharp distinctions between their own efforts to test hypotheses drawn from neoclassical theory and the more descriptive work done by economic historians in history departments. Over time, however, the logic of debates within cliometrics led many of the early practitioners to abandon their strong neoclassical presumptions and adopt more historical, more context-specific approaches in their research.

A good example is the debate over the adoption of the reaper in the United States. Paul David (1966) sparked this literature by modeling farmers as self-contained “firms” which, in accordance with standard theory, chose among alternative technologies on the basis of relative costs. According to this model, farmers would adopt mechanical reapers whenever the cost of purchasing and using them fell below the cost of getting in the crop with traditional hand methods. Because the purchase of a reaper involved high fixed costs relative to hand methods, the larger the farm, the lower the fixed costs of the reaper per unit of production, and the more likely the reaper would be adopted. David collected data on the price of reapers and on labor and other relevant costs and estimated a threshold farm size above which it was more likely that farmers would adopt the reaper. Changes in the relative costs of the two technologies, by his calculations, explained both the reaper's slow diffusion in the 1830s and 1840s and its rapid spread after the mid-1850s.

A number of cliometricians critiqued David's calculations, increasing his estimates of the acreage threshold and thus calling into question his explanation for the timing of the technology's diffusion. Others, however, posed more profound challenges that moved the discussion back toward history. David's model depended on the assumption that each farmer individually decided whether to adopt the reaper. Alan Olmstead (1975) disputed this assumption by examining more traditional historical sources, including the business records of the McCormick Harvesting Machine Company (the most important manufacturer of reapers), farmers' diaries, and advertisements in farm journals (see also Davis 1968, p. 88, quoting historian Alan Bogue). Later he and Paul Rhode (1995) followed up with a more systematic investigation of purchasers of farm equipment recorded in the McCormick Company's sales books. Both studies uncovered considerable evidence that farmers jointly purchased reapers and that some bought reapers with the aim of providing harvesting services to area farmers. The discussion for the most part stopped at this point, in large measure because of the lack of interdisciplinary conversation. One can imagine, though, that if historians had been paying attention there might have been further research on the particular social and cultural contexts that enabled farmers to cooperate. Moreover, such an exploration would have illuminated other important economic issues. David had initially dismissed the possibility that farmers shared reapers, arguing that the time constraint farmers faced at the harvest would have made it difficult to solve such contracting problems as who would get to use the reaper first and how to compensate those whose crops suffered weather damage as a result of having to wait for reaping services (David 1966, pp. 16–17, n27). These problems were assuredly significant. How were they resolved? What role did institutional arrangements or cultural patterns play in facilitating particular solutions? Olmstead and Rhode made enormous progress in answering these and related questions, but presumably historians could have pushed the discussion further.

The literature on the reaper offers a particularly compelling example of the value of moving toward the middle ground because it shows very clearly how combining economic theory with context-specific historical research can shed new light on important economic issues such as the determinants of the diffusion of new technologies. It also suggests how the discussion could have gone in new productive directions if there had been more interdisciplinary discussion. I could cite many, many other examples. For the sake of brevity, I will mention just a few that come from work by members of the first few cohorts of cliometricans. Gavin Wright (1978) sought to explain why small farmers in the antebellum South routinely planted less cotton than would have been profit-maximizing by emphasizing their concern to maintain what historians were then calling a “competence” (see Henretta 1978; Clark 1979; Vickers 1990)—that is, the ability to provide for their families and preserve their status as independent landowners. Robert Fogel (1989) turned to the study of political and religious movements to explain the abolition of slavery in the United States. David (1985), pondering the awkward organization of the QWERTY typewriter keyboard, argued that societies could become locked into particular ways of doing things and find it difficult to shift to alternative technologies, even when it would be more efficient to do so. David and Wright (1997) posited that the economic rise of the United States was resource-based and owed much to a set of institutions and cultural beliefs that encouraged individuals and companies to prospect for mineral deposits, provided them with the necessary scientific expertise, and even subsidized their efforts. Peter Temin (1980) sought to understand why voters in market-oriented societies sometimes quite suddenly shifted preferences and supported economic regulation. He and Barry Eichengreen examined the “mentality of the gold standard” with the aim of explaining why policy makers perversely clung to the gold standard as the world plummeted into depression in the early 1930s (Eichengreen and Temin 2000). Richard Sylla (2002, 2010) turned toward biography (of Alexander Hamilton) to explain the rapid early financial development of the United States.

Some of this work has been embraced by historians and some of it criticized, but mostly it has had little impact. During the period of the cultural turn historians simply stopped paying attention to work in economic history, and there was little that economists could do about it. The lack of interdisciplinary engagement meant, however, that the historical side of the economists' work was often under-realized. Sometimes it was simply proposed as a hypothesis, consistent with the data but not examined directly through the historical record. In other cases, it was fleshed out mainly on the basis of secondary sources. When economists did attempt to develop their arguments with research in archival or textual materials, moreover, the result was often naive. Part of the problem was that investigators tended to look at only the most obvious, or readily available, sources. Part was that they often did not have the language skills to read documents in the original languages but had to rely on translations that missed important nuances. But much of the problem was a lack of appreciation of the skill set required for the analysis of qualitative sources. Although it is certainly true that many historians read documents naively (just as many economists miss the nuances of statistical materials), the best practitioners have years of training and experience that enables them to go beyond the often misleading surface meanings of the sources. They know, for example, how to read texts over and over in the context of related documents until the differences between our modern understandings and those of actors in the past become apparent, how to be on the alert for anomalous passages that reveal assumptions (for example, cultural givens) that the author of the document might not even have been aware of, and how to derive meaning from what was not said as well as from what was said.

In drawing attention to the limitations of cliometricians' historical work, I do not by any means wish to impugn their scholarship. To the contrary, I think their willingness to move to the middle ground should be applauded. My aim, rather, is to emphasize the high levels of expertise required to meet the standards of both of our parent disciplines. Just as one would never expect historians to have the same command of economic theory and econometrics as an economist, one would not expect economists to have the historians' deep knowledge of context and historiography or their skill in interpreting documents. What one can and should expect is for practitioners in both disciplines to internalize the basic respect for each other's training and expertise needed for productive interdisciplinary exchange. The problem, of course, is that decades of intellectual separation have led instead to belittling stereotypes and suspicion. Historians have little or no idea of what economists actually study and too often reduce the discipline to a caricature that is a combination of the basic introductory economics course they struggled with as undergraduates and the economic platitudes spouted by conservative politicians. But economists are just as likely to caricature historians—for example, to see them as captured by the most extreme manifestations of poststructuralist thought.Footnote ²

It is time to move on, and circumstances are now as propitious as they are likely ever to be because historians are returning to the study of topics related to economic history. The first flames of interest seem to have been sparked by Bin Wong and Kenneth Pomeranz's books disrupting conventional notions of the path of Chinese economic development relative to the West (Wong 1997; Pomeranz 2000) and also by Avner Greif's (1989) work on the mechanisms of trade in the medieval Mediterranean. But the financial turbulence of the first decade of the twenty-first century also played a role, and historians are now flocking to study topics related to the history of “capitalism.” The surge of interest in capitalism began in the early- to mid-2000s, when a number of scholars began to write the dissertations that became the books that demarcated the field (Mihm 2007; Hamilton 2008; Moreton 2009; Hyman 2011; Ott 2011), and when Sven Beckert inaugurated his conferences at Harvard on the history of capitalism. But it took on the trappings of a full-blown movement after the financial crisis of 2008.Footnote ³

The scholars who are in the forefront of this movement have backgrounds in cultural history and generally make little use of quantitative sources. Some still operate on the basis of stereotype and are actively hostile to economics without having read much economic history by economists. But none of this is surprising given the long absence of interdisciplinary exchange. As the course of the initially vituperative debates over Wong and Pomeranz's books and also Greif”s work has shown (see the opening salvos by Huang 2002 and Edwards; Ogilvie 2012), the logic of scholarly discussion tends to move practitioners toward the middle. Thus there is now a large and largely informative interdisciplinary literature on the different growth paths followed by western countries compared to Asia and elsewhere (see, for examples, Coclanis 2006; Berg 2004; Goldstone 2002). There is also an increasingly illuminating literature on the conduct of long-distance trade in medieval and early modern times (Trivellato 2009; Goldberg 2012; Lydon 2009). My sense from my own personal conversations with scholars who consider themselves historians of capitalism is that they are increasingly feeling a similar pull toward the middle and are interested in developing a more sophisticated understanding of economic thinking and in getting up to speed on economic history literature relevant to their research interests. I expect this tendency to continue as debate over some of the recent big books in the history of capitalism. I am thinking in particular of Edward Baptist's Baptist's The Half Has Never Been Told (2014), but also Sven Beckert's Empire of Cotton (2014) and Walter Johnson's River of Dark Dreams (2013) reveals the significant errors that resulted from the authors' lack of economic intuition or knowledge of research findings bearing on their topics.

I would like to conclude by emphasizing that economists need interdisciplinary exchange with historians as much as do the historians of capitalism. They need it especially because of their rapidly growing interest in the persistent effects of past institutions and cultural practices on economic outcomes in the present (see, for examples, Nunn 2008; Nunn and Wantchekon 2011; Alesina, Giuliano, and Nunn 2013). There is much that is problematic about this literature from the standpoint of scientific method. Articles only get published when they report statistically significant results; negative findings never see the light of day. Hence the literature ignores cultural practices and institutions that do not have lasting effects, even though they may have been important shapers of economic behavior for long periods of time. At the same time, the literature simply assumes that practices and institutions that have significant associations with outcomes in the present were always important. Understanding how and why some cultural practices persist and others do not, and the circumstances under which they rise and fall in importance, would seem to be important items for economic history's future agenda. Formal modeling and hypothesis testing are obviously in order, but to be productive they will have to be informed by the deep knowledge of culture and institutions that are the historians' stock and trade. We can all think of cultural phenomena that seemed to be very persistent, very difficult to change, and then suddenly they gave way. Culture is not fate, and neither are the disciplinary practices that prevent economists and historians from improving each other's scholarship.