The GOVERNANCE blog

Robert F. Durant responds to Don Kettl’s commentary on the neglect of big questions in public administration: As usual, Don Kettl makes several excellent points in his commentary about the so-called “big questions” in public administration and public management. As one of those who has written about and lectured on the negative impacts of general trends in the field on junior (and senior) scholars (1), I would add a friendly amendment to his point regarding the rewards to be gained by addressing big questions.

To address the problem requires more than accurately pointing out that Simon or others of his era focused on big questions and garnered big professional rewards from doing so. Scholars—new and seasoned—face a very different set of incentive structures as professionals today than did those in Simon’s day, or even two decades ago. Nor is it sufficient to say that data sets are available that could inform these issues. Because of the inherent statistical and data-collection limitations of econometric approaches to the study of public administration, as well as the tendency of these techniques to be ill-suited to the study of the large-scale, slow-moving, secular forces that are often the essence of big-picture questions, big questions get pushed to the back burner of contemporary research agendas. Consequently, exhortation will fail unless the field understands and addresses the perverse incentive structures existing today that not only make junior scholars feel this way but also deflect their research attention away from big questions in the first place.

These interrelated disincentives include, but are not limited to, (1) a ticking tenure clock for junior faculty and its relation to the study of big questions, (2) the overwhelming focus on adding statistical methods courses to PhD coursework at the cost of more big-picture-oriented classes, (3) stiffening competition for journal space, (4) the commodification of scholarly worth in measures of citation rates, and (5) the emphasis in leading research universities on grants from foundations and other funding sources. Together, they afford major disincentives to focusing on big-picture questions.

For starters, the nature of big-picture research often depends—because of data gaps when attempting longitudinal analyses and data collected to answer different questions—on qualitative, archival research that is more time consuming, has more dead ends, requires process-tracing over time, and is more difficult to condense into journal articles without losing key explanatory context. It is thus quicker to find an existing data set rather than create a new one, to identify questions that approximate (but may not precisely operationalize) big-picture questions (such as questions in the Federal Viewpoint Survey), and to send out multiple manuscripts using econometric analyses as quickly as possible to journals as the tenure clock ticks down.

This tendency is reinforced by the expanding emphasis on econometric analyses in most PhD programs in the United States; one does what one is trained to do in PhD programs. Without question, and as Don notes, these methodologies have made significant contributions to our understanding of public administration and public management. A good portion of my own research has used these methods. But the clear message being sent to students in PhD programs is that econometric analyses are the epistemology of choice for making reputations. Perhaps that is true today; perhaps not. But it certainly guarantees that it will be the case in the future, because many big questions in our field require qualitative analyses or mixed methods. Even more significantly, we should understand that there are enduring questions that econometrics cannot address because of the aforementioned data gaps and mathematical limitations inherent in them when it comes to addressing large-scale, slow-moving, secular forces. Consequently, we are “hollowing out” both the breadth of the field and the validity of our answers to its big questions by decontextualizing and de-historicizing how they are studied in the pursuit of econometric parsimony.

Moreover, many schools of public affairs increasingly are staffed partly by fields that do not value books (e.g., economics) compared to their value in Simon’s era (or even several decades ago) and have moved toward that field’s dissertation model of “three papers” rather than book-length manuscripts. Thus, the allure—as well as the skills necessary to address big questions requiring the development of extended and empirically supported arguments—diminishes. This is compounded by journal editors’ understandable concerns over the allocation of precious space in journals, as greater numbers of manuscripts arrive on their desktops. This is not to say that the big questions are not attractive to editors, but that the bar is high for marshalling evidence to support big-question claims given space concerns. Of course, a supply-side problem for journal editors may also be at work because of the disincentives I am identifying.

The commodification of scholarly and professional worth pursued by most American research universities today also creates disincentives for research on big-picture questions. It also creates disincentives for anything but methodological and econometric innovation. For instance, although leading research universities do not expect large numbers of citations from junior faculty, they increasingly require data on citations in promotion and tenure dossiers. Moreover, with Charles Dicken’s “Mr. Gradgrind” apparently in charge today of establishing the professional value of a faculty member’s scholarly reputation, junior and senior faculty have an incentive for publishing in well-worn paths, as established in the journals and by available data sets, so they can maximize citation counts. Moreover, this is happening despite caveats associated with using them in this way by entities such as Google Scholar, which collect these data. To take a substantively innovative or untrodden topical path could mean jeopardizing one’s long-term reputation as long as inordinate weight is put on citation counts. Meanwhile, as bringing in grant money in sizeable amounts from major public and private funders becomes yet another component of junior (and senior) faculty evaluations, what these entities fund becomes part of the incentive structure for scholars. These funders are not known for a focus on the “big questions” of public administration and public management.

Thus, I too have argued in the past that reputations are to be made by addressing the big questions in our field. But I have also argued that the roots of this problem are as numerous and multifaceted as the “big-questions” themselves. As long as these disincentives exist, junior (and senior) scholars are likely to be cautious about pursuing research on “big questions.” So, in my judgment, the field needs either to disabuse PhD and junior faculty that these barriers are real, establish journals with high levels of legitimacy that deal with broader theoretical and conceptual issues in the field (PMRA’s announced new journal may help in this regard), and/or work to revise these perverse incentives accordingly.

(1) See, for example, Robert F. Durant, “Taking Time Seriously: Progressivism, the Business–Social Science Nexus, and the Paradox of American Administrative Reform,” PS: Political Science & Politics 47, no. 1 (January 2014): 8-18. Originally presented as the John M. Gaus Award Lecture, American Political Science Association, September 2013.

Robert F. Durant is Professor Emeritus of Public Administration at American University.  In 2013, he received the John Gaus Award for a lifetime of exemplary research in the joint tradition of public administration and political science.