Anvil or Wellspring? The Use of History in Legislative Studies

Daniel Carpenter
University of Michigan ¹

With a few exceptions, congressional scholars seem primarily to have embraced the anvil metaphor in practicing history. In the interest of provocation, I claim here that they have done so at real cost, and that the most promising future for historically oriented legislative research lies in using history as a theory-building and data-type-expanding tool, or, perhaps optimally, some mixture of history as anvil and as wellspring.

The Narrative Method as a Wellspring of Theory

I start with a simple question: what do historians (academic and otherwise) do? A rich literature struggles with that question, but here I shall state the obvious. Historians do not simply study "history" as a collection of "old" facts. They tell stories. The wellspring notion of history that I'm defending sees narrative at the core of the political science enterprise.

At its best, well-conducted narrative research presents an opportunity for new theory building. Being built from contemporary examples, our theories might be blind to strategies we haven't witnessed, e.g., William Riker's heresthetic (Riker 1983), of which his best example was Chauncey DePew's blockage of the Seventeenth Amendment; institutional possibilities we hadn't imagined, e.g., the creation of appropriations committees as a centralizing mechanism (Stewart 1988); causal factors that we had previously ignored, e.g., the role of government fiscal policy in the decline of parties (Coleman 1996); or stylized facts that seem to be promising candidates for theoretical explanation, e.g., the productivity of divided governments (Mayhew 1996), the persistence of antistatist parties signing off on state-building regulatory legislation (James 2000).²

At its most promising, this research is inductive, at least in part. By "inductive" I mean research that does not set out to disconfirm or confirm any single theory or set of theories, but rather aims to expand our knowledge base. Inductive narrative in this way seeks anomalies, not simply facts or patterns that seem irreconcilable with the theory-du-jour, but also factual surprises that call into question our presuppositions about institutions and the actors they constrain and enable (e.g., Mayhew 1996).

As historical research progresses, different types of narratives emerge. Daniel Rodgers' Atlantic Crossings (Rodgers 1998) offers a shining example of how a focus upon the cross-national flow of ideas, strategies, and policy options can explain previously anomalous patterns of institutional and cultural change. Why did Progressive Era items such as national health insurance, arid lands reclamation, and utilities municipalization make near simultaneous appearances on the policymaking agendas of numerous countries with very disparate institutions, economic situations, and national cultures? Rodgers shows that a "Progressive Atlantic network" of connections among American and European politicians, activists and intellectuals accounts for much of the political agenda during this period. Rodgers' argument compels historical researchers in political science to consider cross-national influences upon institutional change. Numerous congressional institutions, policy choices, and party structures now await a Rodgers-style analysis; civil service reform, ballot and electoral reform (e.g., the Australian ballot), and regulatory reform in the Gilded Age and Progressive Era are a few of many possible examples.

Is this indeed the way that sound theory is built? Can inductive historical research play a role? If so, should it? Since contemporary political scientists seem reluctant to embrace any model or research practice unless economists have hugged it first, consider the following counterfactual queries from the recent history of academic economics. Would economists such as Paul Krugman have spun theories of urban development in the past ten years were it not for research in economic history and geography showing the concentration of economic growth in urban areas and their surrounding regions? Would they have turned to the relationship between institutions and economic growth were it not for Douglass North's macro-historical research showing a relationship between the two? Would political scientists and economists have converged to build the capture theory of regulation in the absence of Samuel Huntington's analyses of the early ICC or George Stigler's study of 1920s state trucking regulation? The answer to all these questions is no. Theoretical developments across the social sciences have been driven by inductive historical research.

Nothing about the wellspring alternative, moreover, commits it to history-dependent reality. Some facets of a static "real world" may be more observable at some times than at others; if so, historical research will yield a higher probability of scientifically discovering those realities. Alternatively, in a world with Polya-urn path dependence (Pierson 2000), choices at one time will determine the opportunity set later on. Hence any accurate model of the process (and any scientific research) must incorporate an historical approach, viz., one which considers the sequence of action and describes explicitly how actions taken at time t limited (or perhaps expanded) the feasible set of opportunities at time t + k.

The Narrative as Wellspring of Empirical Method

The other grand hope of historically oriented legislative research is that it will lead us not simply to new data, but to new forms of data. Consider Jonathan Katz's and Brian Sala's analysis of congressional committee tenures and how they began to rise after the introduction of Australian ballot reform in the early 1890s (Katz and Sala 1996). In a world dominated by studies of contemporary congresses, it is not clear how political scientists would ever have found the need to analyze this sort of data. Katz and Sala's study, it is worth pointing out, is far from simple analysis of the determinants of congressional committee tenures. The kernel of their analysis was the identification of an upward historical shift in the mean of the tenure distribution, such that the induced incentives to specialize that ensued from ballot reform engendered longer and longer stays on House committees. It is hindsight at best, but I venture to say that a non-historical examination of committee tenures would not have identified these specialization incentives as rapidly or as sharply.

Of course congressional history will also give us thousands new votes to analyze, a different panoply committees to study, new ("old") faces in congressional leadership, and the like. Studies of these phenomena will continue to be valuable. Yet I think that the real promise of historically oriented congressional research lies elsewhere.

Exactly what new forms of data shall arise I do not know. One sure source for them will be found in the recently opened legislative archives at the National Archives. The Archives has recently made available to the public dozens of committee-specific archives, including valuable committee journals where daily proceedings, participation and committee votes were recorded, and bill-specific files where petitions and other lobbying materials were deposited. I have used some of this material in my research,³ but most all of it remains unused. Since committee votes were not customarily reported until after 1970 - remaining known only to keepers of the committee files or enterprising reporters - there may be some useful natural experiments to consider regarding committee versus floor voting strategies that are uniquely testable given this data. I leave it to my colleagues in legislative politics to use these empirical reservoirs in more creative ways.

Conclusion

For all of this criticism, I am still impelled towards the conclusion that students of Congress have better engaged with history than have students of bureaucratic politics. Very little if any of the recent work in bureaucratic politics - most all of it chained to vague principal-agent models and concerned purely with agencies of the past two decades - has undertaken to study agencies older than 20 or 30 years. Where scholars of the bureaucracy have chosen to analyze bureaucratic or regulatory "history," they usually do so indirectly by studying their creation. (Witness the dozens-fold studies of the ICC, the FTC and their enabling acts.) Partial exceptions exist to this pattern - among them the work of Lawrence Rothenberg and Scott James (2000) - but they are exceptions that prove the rule. At the very least, then, congressional scholars are studyingcongressional history.

As I have argued here, however, the real promise of the historical turn in legislative research lies in seeing history as a wellspring of new theory and new forms of data. To the degree that congressional scholars restrict themselves to the anvil model and take their existing theories and forms of data to older periods, they will certainly produce publications, but they will also miss an opportunity to build richer and truly home-grown theories of institutions and institutional change.

Notes

1. I note here an important caveat: I am not primarily a congressional scholar but instead labor in the fields of bureaucratic politics, regulatory politics and American political development. Much of my research has, however, taken me to congressional archives and has involved the use of theories of Congress and congressional data. In addition, studying Congress is a necessary part of any study of bureaucratic politics. I also believe the reverse is true. At least in the Gilded Age and Progressive Era, strategic bureaucratic action often induced changes in legislative institutions and legislative choice; see Daniel P. Carpenter, The Forging of Bureaucratic Autonomy: Networks, Reputations and Policy Innovation in Executive Agencies, 1862-1928 (Princeton: Princeton University Press, 2001).

2. I cite Riker here because he is often hoisted as the exemplar and founder of deductive, rational-choice based thinking in political science. Yet it is also interesting how the inductive use of history in theory building permeates much of his later work. It is also worth mentioning that Riker's early work was of an intensively historical variety; see his study of the National Guard (Riker 1957).

3. See The Forging of Bureaucratic Autonomy and "State Building through Reputation Building: Coalitions of Esteem and Program Innovation in the National Postal System, 1883-1913," Studies in American Political Development 14 (Fall 2000): 121-55. I consulted the archives of about ten committees, mainly for the purpose of retrieving bill-specific files.

References

Carpenter, Daniel P. 2001. The Forging of Bureaucratic Autonomy: Reputations, Networks and Policy Innovation in Executive Agencies, 1862-1928. Princeton: Princeton University Press.

Coleman, John J. 1996. Party Decline in America: Policy, Politics, and the Fiscal State. Princeton: Princeton University Press.

James, Scott C. 2000. Presidents, Parties, and the State: A Party System Perspective on Democratic Regulatory Choice, 1884-1936. New York: Cambridge University Press.

Katz, Jonathan N. and Brian R. Sala. 1996. "Careerism, Committee Assignments, and the Electoral Connection." American Political Science Review 90 (March) 21.

Mayhew, David. 1996. Divided We Govern. New Haven: Yale University Press.

Pierson, Paul. 2000. "Increasing Returns, Path Dependence, and the Study of Politics." American Political Science Review 94, 2 (June]: 251-268.

Riker, William H. 1957. Soldiers of the States: The Role of the National Guard in American Democracy. Washington, DC: Public Affairs Press.

Riker, William H. 1983. The Art of Political Manipulation. New Haven: Yale University Press.

Rodgers, Daniel T. 1998. Atlantic Crossings: Social Politics in a Progressive Age. Cambridge, Massachusetts: Harvard University Press.

Stewart III, Charles. 1989. Budget Reform Politics: The Design of the Appropriations Process in the House of Representatives, 1865-1921. New York: Cambridge University Press.