Problem-driven Research in Regional Science

Introduction

During his thirty-five years as a regional scientist, applied economist, and urban and regional planning professor, Andrew Isserman made significant, durable contributions to our field and to related social and policy sciences. Although he loved methods and was embarked on early stages of a regional methods book, his work was heavily shaped but what he saw as important real-world questions that he felt called upon to tackle: the decline of small towns, rural poverty, immigration, energy, and environmental issues. He often set his sights on existing policies and institutions such as interstate highways, military bases, and the Appalachian Regional Commission.

Isserman believed in big ideas, in evidence, and in being of service. He loved data and spent years improving public data sets. He adapted existing and designed new methods to test regional development interventions and their efficacy. He served as policy advisor to a large number of diverse agencies at state and federal levels, and helped Eastern Europeans and Russians think through their regional agendas once the iron Curtain fell.

Isserman was also an intentional shaper of our field, regional science. In addition to his work as research and thinker, he was a field builder. Colleague to many and invisible editor for many more, he played a lead role in creating and carrying forward the International Regional Science Review (IRSR). He took over from Bill Miernyk in building the Regional Research Institute at University of West Virginia. He nurtured students and postdocs who now apply his broad and powerful ideas and methods to new areas of research.

In this article, I summarize research conducted for the Andrew Isserman Lecture, given at the annual North American Regional Science Association meetings in 2011. I explore the role of problem-driven research in regional science with particular reference to Isserman’s work. Why is problem-driven research important? Because it may improve the lives of regional residents and help regional economies perform better. Tackling a problem that begs for a solution can redirect our time and skills toward knottier problems than our preference for pure and clever exercises would tolerate. We know many regions face severe challenges, from outmigration to environmental degradation. Placing real-world problems at the core in fashioning our research questions is likely to force us to consider complex causalities even if we cannot arbitrate among them fully.

One way to understand the place of problem-based research in regional science is to review its history since the founding of our interdisciplinary discipline. Calls for greater problem-driven research design in regional science are periodically asserted. They emerged as early as 1975 in the launching of the IRSR. In designing the new IRSR and shepherding Isserman into its leadership role, Walter Isard chartered the journal to go beyond a methods-driven approach and to address important societal questions. For regional science in general, these missions have been reasserted periodically, including in Isserman’s (1993) “Lost in Space?” article in the Review of Regional Studies and in my North American Rangers Supporters Association Presidential lecture of 2001 (2002).

In what follows, I distinguish problem-driven research from methods-driven work, long dominant in regional science. Using economic base theory and associated multipliers as examples, I suggest that methods-driven research can be misleading and damaging to regional economic development, especially by stifling other avenues for theorizing and policy experimentation. I revisit the debut of the IRSR to underscore Isard’s, and later Isserman’s, visions for the journal, and highlight, over the decades, prominent examples of problem-driven research published in it. I then use Isserman’s and others’ research in regional science to explore features of exemplary problem-driven research. After speculating on the reasons for the popularity of methods-driven research, including the prominence of economists and geographers in this interdisciplinary field and the relative absence of other social scientists (political scientists, sociologists, anthropologists), I conclude with several ways that regional scientists can encourage more quality problem-driven research.

Problem-driven Aspirations: The IRSR’s Origins

Early regional science spanned both theory and method innovations. Isard’s (1956) Location and Space Economy was an elegant inquiry into why firms locate where they do, building on earlier, primarily German, location theorists—arguably a problem-driven exercise. Alonso’s (1964) metropolitan twist on location theory asked why land prices declined (and the size of residential parcels increased) with distance from the urban core. But by far the most popular of Walter Isard and his students’ seminal innovations were the basic tools presented in Isard’s (1960) Methods of Regional Science.

Isard once explained to me in an interview that he had really not begun with the idea of regional science at all. A Quaker and antiwar activist during World War II, he really wanted to establish peace science. But the McCarthyism of the times made this difficult. Though he did eventually start a Journal of Peace Science, his defining contributions have been regional science, including its theories, methods, institution building, and internationalism.

Isard did, however, have real-world aspirations for regional science. In the early 1970s, as David Boyce recounted at the University of Illinois Isserman Symposium talk:

During this period Walter Isard wanted to establish another regional science journal, which would report on applied research with policy implications. He asked me if I knew of a young scholar who might be interested in editing this journal. I responded yes, and his name is Andrew Isserman. (2011)

Without consulting the Regional Science Council, Walter, with Roger Van Zele, produced the first issue of the IRSR in spring 1975. Inside the front cover, Isard penned the following ambitions for IRSR:

The International Regional Science Review aims to focus on multi-disciplinary research regarding policy issues and questions—an aspect of regional science which has been relatively neglected. The Review will have only a secondary interest in theoretical research, analytical techniques and models per se. Also, it shall emphasize problems of international interest rather than those specific to any particular nation or region of a nation. Thus much attention will be given to general questions of regional development, environmental management, resource use and urbanization and to substantive research pertinent for planning and decision-making. The editors particularly wish to have contributions from young scholars with innovative, creative ideas, even if highly unorthodox and not yet fully tested empirically (Isard 1975).

Isserman did agree to take on the IRSR editorship, an astonishing project for an assistant professor. With support from his department at University of Illinois Urbana–Champaign, Isserman edited and produced Volume 1, Number 2 of IRSR in the fall of 1976. He edited the journal from 1976 to 2008, sometimes with coeditors (1980s) and subsequently with coeditor and successor Luc Anselin.

The birth of urban economics as a field in the 1960s spawned a parallel stream of policy-directed research, quickened by new public sector research and evaluation funding associated with federal urban redevelopment and Great Society programs. For instance, Rutgers Center for Urban Policy Research (CUPR) was founded in 1969 and ably led for decades by George Sternlieb (doctorate in business) and Norm Glickman (PhD in regional science, Penn). Through 2011, CUPR completed over US$40 million worth of research for governments (including NSF) and private foundations on affordable housing, land use policy, environmental impact analysis, state planning, public finance, land development practice, historic preservation, infrastructure assessment, development impact analysis, the costs of sprawl, transportation information systems, environmental impacts, and community economic development. Other universities—Brown, Massachusetts Institute of Technology, Penn, UC Berkeley, Northwestern—spawned productive urban research centers as well.

How well has regional science delivered on Walter Isard’s call for a focus on multidisciplinary research regarding policy issues and questions? Has the review cultivated this emphasis? And more importantly, are regional scientists teaching problem-driven research and addressing important policy issues in their work?

Problem-driven and Methods-driven Research Defined

Although Isard’s call used the word question, I prefer to use problem in describing this type of research strategy. While questions posed in research can often be simply factual, the focus here is on broader societal quandaries and deficits that can benefit from causal research findings. Problem-driven research in regional science starts by posing a question about spatial or place-based phenomena and strives to answer it with reasoning, evidence, and methods appropriate to the question. The problems should be important rather than trivial ones, and the research design should aspire to explore causality and explanation, not just description. Often, we tag on short policy implications sections late in our articles. But in good problem-driven research, the problems should be posed at the beginning of the article or project, their significance underscored, and the methods of research chosen for their power to yield answers. Successful research conducted under these circumstances should yield insights that are useful to organizations and policy makers who want to improve cities, towns, and regions. Their policy concerns should be articulated at the outset of the research project, not as an afterthought.

Problem-driven research often states (or could state) a question in its title. Examples are Markusen’s (1986a) Defense Spending: A Successful Industrial Policy? Isserman’s (1993) Lost in Space? On the History, Status and Future of Regional Science, and Foad's (2010) Europe Without Borders? The Effect of the Euro on Price Convergence. Even books can be framed with policy questions, as in Markusen, DiGiovanna, and Leary’s (2003) From Defence to Development? Many other research articles refer to policy problems in their titles or abstracts. Problem-driven research can be theoretical—proposing an alternative theory—but should be testable and is more satisfying when held to evidence.

We have all probably heard some version of the story about the professor who, on a dark and foggy night, leaves the pub after a couple of beers, only to reappear to tell his colleague that he has lost his car keys. After fruitlessly searching around the table, the colleague goes out to help his friend. The first fellow concentrates on a sidewalk area that is under a street lamp curiously far from his car. Would not they likely be close by your car? asks the colleague? Well, yes says the other, but this is where the light is! The question—where are my keys?—is not addressed in the first instance by reasoning and superior data but by the convenience of a tool.

In regional science, methods-driven research starts by proposing, improving, or applying any one of a growing toolkit of spatial or region-oriented methods to a particular region, set of regions, interrelationships among regions, or spatial phenomena generally to produce extensions and results not organized around a policy or otherwise important problem. The tools are like the lamplight. They enable us to explore certain features and not others. When we start our research process with a tool, rather than a problem, we are doing methods-driven research.

This duality—problem- versus methods-driven—is crudely constructed. A good research project/article could be both. A problem-driven hypothesis could result in a methodological innovation, or a methods-improving effort could help others obtain answers to important problems. Clearly, improving methods is desirable, and research that proposes to do so is legitimate. It is not the practice of methods-driven research per se that this article critiques, but its dominance in regional science research, publication, and teaching.

The Use and Misuse of Economic Impact Multipliers

Excessive methods-driven research and practice can hamper a fuller investigation of pressing regional development issues and appropriate policy solutions. For instance, the economic development conundrum of job creation in many cities, towns, and regions is often dealt with by searching for economic (or export) base industries and trying in incentivize their expansion, including through recruitment. The operational idea, perceived by public practitioners and even the general public, is that the only good job is one that produces a product or service that is sold outside of the region (or to a tourist who is temporarily on site). Generations of master’s of planning students have been taught how to compute and use economic base multipliers, often stripped of any linkage to underlying theory and debate.

What is the causal theory behind such multipliers? The seminal debate on export base theory was conducted by Douglas North and Charles Tiebout in the 1950s. Economic historian North, then teaching at the University of Washington and likely influenced by Canadian Innis’ (1930) staples theory, argued that a region’s growth is constrained by its ability to export (North 1955). Income from exports is then circulated to local workers and suppliers (indirect effects) who then respend it, at least in part, in the regional economy. Also at University of Washington, Tiebout (1956), in a brilliant critique, pointed out the logical flaw in this argument: the world economy as a whole does not export, yet continues to grow. He posited, among other critiques, that an elaborating internal division of labor could produce growth, echoing Adam Smith’s famous characterization of capitalist production and trade. Other economists also expressed skepticism.

As evidence, North (1961) subsequently wrote an account of nineteenth-century (1790–1860) American economic growth in which he argued that most of the growth of that period could be attributed to slave-grown cotton exports. Following Tiebout’s reasoning, one might stress instead (or in addition) an elaborating internal division of labor: the synergy between highly productive family farms and a manufacturing sector hiring hungry urban nonfarm workers and finding lucrative markets in farm implements. Economic historian Lindstrom’s (1978) book on the Philadelphia region from 1810 to 1850 provides evidence of the dominance of such within-region rural/urban division of labor, supporting a Tiebout-style interpretation.

Export growth may follow rather than lead output growth. Over subsequent decades, a number of economists constructed cross-sectional and longitudinal tests of the export base hypothesis using nations as units. For thirty-seven developing countries over the period 1950–1981, Jung and Marshall (1985) found that evidence supported the export promotion thesis in only four cases. Five countries grew but reduced exports, while four countries experienced export growth but output reduction. Ghartey (1993) concluded that export-driven development appeared to explain growth in Taiwan but not Japan or the United States. In a five-country study, Sharma, Norris, and Wai-Wah-Cheung (1991) found that Japan and Germany experienced export-led growth from 1960 to 1987, but in the United States and the United Kingdom, output growth induced export growth.

Through the mid-1990s, there was no compelling evidence that exports drove overall growth. Policy-induced accelerated economic integration (North American Free Trade Agreement, General Agreement on Trade and Tariffs rounds) since the early part of that decade may have made exports more prominent for nations and regions. Yet, there are good reasons and some evidence to suggest that investments in local-serving sectors may produce sustainable jobs.

Several alternative hypotheses have been advanced. For one, an innovation aimed at a local market might prove itself locally and evolve into an exported product or service (Cortright 2002). Second, people are also mobile and may choose to live in a particular place for its amenities but bring their asset income or entitlements (like social security) earned elsewhere (Nelson and Beyers 1998). Third, secular changes in consumption patterns, linked to demographic characteristics such as aging or labor force participation decisions on the part of two-parent households, may result in disproportionate demand for high quality of life working and living arrangements, creating more local-serving activities industries. Markusen and Schrock (2006) found that over the 1980–2000 period, the local-serving occupations in the thirty largest US metros outpaced job growth in export base occupations by four to one. For more general treatment of the potential for local-serving economic development investments to sustain produce job and output expansion, see Markusen (2007a), Markusen and Schrock (2009), and Markusen, Gadwa-Nicodemus, and Barbour 2013).

Despite vigorous theoretical debate and very mixed empirical evidence, export base methods still dominate economic development practice in the United States and elsewhere. Although the methods themselves have been subject to decades of tinkering, especially on how to identify and measure the economic base, most practitioners use them in their rawest form, without reference to the theoretical debates or extant evidence. Local consumption is still assumed to move in lock step with export base growth, and economic development policies favor businesses that export their output rather than serve local markets.

In a final irony, the evidence is incontrovertible that output for local consumption grows faster than export output as a town grows into a city and a city into a metropolis. In other words, the multiplier is not stable—the ratios of local-to-export employment and output increase disproportionately. Furthermore, the expansion in the local consumption base increases faster in some regions than in others of the same size. Yet, state and local economic development policy remains myopic about the value of investments in local-serving capacity. The lion’s share of business incentives, whether direct spending or tax expenditures, goes to companies who will build or expand to export out of the region (Markusen 2007b). In answer to the problem “how can a region create jobs,” regional scientists, economist, and planners have generated excellent reasoning and rich evidence that is mostly ignored by public sector economic developers.

Problem-driven Research in the IRSR

How much problem-driven research has been published in regional science? We might, as one anonymous reviewer suggests, use the criterion of intentionality to determine this, surveying authors about their motivation for undertaking research. We might also use bibliometrics, using electronic tools to sort through texts, conduct content analysis, and gauge networks and influence (see e.g., Maier 2006). However, it is quite possible that readers might better assess problem orientation by actually reading the articles. The same reviewer recalls that the IRSR once published a subject–author index that included categories like spatial modeling, methods, and policy areas that might have, had it continued, formed the basis for such an inquiry. For this article, I chose one journal that self-consciously aspired to publishing problem-relevant research—the IRSR—investigating its stated ambitions at the start and reading through abstracts of articles in selected (randomly) years along its trajectory. The method is exploratory rather than conclusive.

Compared with other regional science journals, the IRSR has had, in its origins and editorial leadership, an ongoing commitment to problem-driven research. Has the IRSR lived up to the mission of its founders? Despite Walter Isard’s aspirations for the IRSR, his own first contribution (Isard and Van Zele 1975) reveals a tools-driven format. Consider these lines from the opening paragraph:

In this paper, we wish to present systematically some of the basic techniques which we judge to be highly relevant for environmental management studies …. Our aim … is to summarize the state of the art…. (and) to set down a methodology which can help form a basis for traditional decision-making regarding environmental management. (Isard and Van Zele 1975, 1)

The article intends to be useful to policy makers, but only by showcasing existing techniques.

To gauge the balance between problem-driven and methods-driven articles in the review, I scanned the titles and abstracts for all articles in four periods: the first three years of the review (1976–1978), the late 1980s (1987–1989), the late 1990s (1998–2000), and the three most recent issues (2009–2011). I did not read the entirety of articles, which might have revealed more mixing of the two approaches. Indeed, I would not be surprised if problem-driven research articles often made methodological contributions, driven by the need to generate real-world answers. And, too, some of the methods-driven pieces may have enabled important new policy insights, either by their authors or others.

Reviewing titles and abstracts, I found quite a few articles whose titles and contents run something like this: an X method for accomplishing Y: An application to Z region. Many others worked on specific regional methods, offering conceptual and application contributions. The types of articles published did change over the decades. In the first few years, articles of both types were more purely descriptive than in later decades. For instance, an article by Moffitt (1977) asked whether city/suburban wage differentials had decreased with population dispersion—he found they had not.

In the journal’s first few years, very few articles were explicitly problem-driven. The exceptions, however, show the potential for regional science to contribute to policy making. Sandoval and McHugh (1976) asked whether state economies, particularly their industry mixes, were responsive to energy prices and policy changes. Their answer may indeed have positively informed policy making. Addressing how to deter crime in small communities, Hakim, Ovadia, and Weinblatt (1978) found that some community features, such as wealth level and commercial activity, are associated with greater incidence of crime, but that policing effectiveness lowered crime rates, a finding that supports improvements in policing practices.

As the journal matured, Editor Isserman took a more proactive role in generating policy-relevant, interdisciplinary and international content. It was not enough to simply send out for review what came across the transom. Isserman, reflects current Editor Serge Rey, became an evangelist of sorts, seeking out people who would organize special issues, especially those that met the Journal’s founding aspirations. An excellent example is the 1987 special issue that Roger Bolton put together entitled “Regional Aspects of the Chinese Economic Reforms.” Bolton (1987), writing his introduction during the critical 1987 Party Congress that “apparently has preserved the momentum of change toward freer markets and individual incentives,” assembled articles from two geographers, three economist, and two political scientists. Some of the articles are mainly descriptive, but others engage in policy analyses of resource allocation and deliberate regional restructuring efforts.

Most other articles published in the 1987–1999 issues concentrate on descriptive patterns of regional and spatial differentiation and on methodological innovations. The second IRSR issue of 1989 contains several articles that assess the policies to slow the growth of megacities in the developing world, including contributions by planning professor Townroe (1989) and geographers Brown and Lawson (1989), another set that satisfy the international and interdisciplinary as well as problem-solving criteria.

In 1998–2000 IRSR issues, interdisciplinary and problem-solving articles in the IRSR occur in patterns similar to those of prior decades' end issues. In the first issue of 2000, I worked with colleagues to produce a series of articles on how post-Cold War defense cuts were being handled by national governments and regions with heavily defense reliance (Markusen and Brzoska 2000, of which more below). The articles, written by economists, planners, geographers, and other social scientists, stretched from Russia and East Central Europe to Italy, the Netherlands, Belgium, Germany, and France, and included American shipbuilding and aerospace regions. All scrutinized the structures and policies that shaped the relative success of each region in parlaying people, technologies, structures, and land into other productive uses. The first issue of 2001 focused on policies for rural America, and included contributions from researchers outside of the academy and policy makers like Mark Drabenstott of the Center for the Study of Rural America, Alan Greenspan, Federal Reserve Board Chair, and Ray Marshall, Secretary of Labor as well as an Italian contributor summarizing Organization for Economic Cooperation and Development rural policy lessons (Pezzini 2001).

An anonymous reviewer reminds us of two Isserman insights into why the IRSR did not live up to Walter Isard’s aspirations, at least in its first couple of decades. In his “Lost in Space” overview of regional science past and future (2003), Isserman wrote: “The International Regional Science Review had to abandon an early goal of being a policy-oriented journal because there was not enough good policy research being done by regional scientists.” In his undelivered Southern Regional Science Association address, Isserman (2010) makes the remarkable statement: “Walter Isard once told me when I was its editor, that the International Regional Science Review is a fine journal, but not regional science.” These statements reflect the self-selectivity of those attracted to regional science and their resistance to problem-driven or policy research, despite a welcoming outlet for this type of research, something to revisit and ponder. The latter quote also suggests fuzziness and mixed messaging in the definition and bounding of regional science, even in the view of its founder.

In recent years, under new editorship, the IRSR has published a number of policy-relevant articles, often explicitly problem-driven. Two 2010 articles ask questions central to regional policy making. Foad’s (2010) “Europe Without Borders? The Effect of the Euro on Price Convergence” explores whether currency unions make a difference to cross-border price stability. Foad analyzes how prices differ between a country and its bordering neighbors, and how the differences move over time, that is, how volatile the differences are. For a large set of European countries, he finds that the currency union has reduced the volatility of such price differences between member countries, especially where the largest Euro countries are concerned. In contrast, price volatility for the United Kingdom, not a Euro Zone member, has increased. The results strongly vindicate the Euro Zone construct, at least for this particular policy goal.

Another article, Batabyal and Nijkamp’s (2010) “Asymmetric Information, Entrepreneurial Activity, and the Scope of Fiscal Policy in an Open Regional Economy,” asks whether fiscal policy in an open regional economy can be successful in boosting entrepreneurship. While they confirm the potential of venture capital to do so, they find that regional public authorities will find it difficult to incentivize more entrepreneurship because their access to good information is poor compared with the private sector’s access. Their findings are discouraging and thus of importance to regions considering the use of fiscal policy to meet this goal.

Continuing its tradition of special issues, the IRSR published a remarkable collection of articles in 2009 on role of research in state-level policy making. In their introduction, special issue editors Hirasuna and Hanson (2009), they state: “this issue examines how regional science research gets used in the policy process.” Their contributors include regional scientists specializing in energy, environment, urban development, rural development, welfare, and poverty. Summarizing across this wide set of contexts, they enumerate why getting policy makers to pay attention to and use one’s research is difficult. One, work incentives and styles are different for policy makers than those that govern academic research protocols. Two, developing mutual respect takes time, resources, know-how, and the building of relationships. They conclude that there are two routes for influencing policy: an indirect one, through teaching (including preparing future policymakers) and disseminating research results through organizations, consultants, businesses, and think tanks, and a more direct one that involves working directly with state legislators and executive branch leaders and their staffs.

Over the decades, Andrew Isserman and subsequent editors have encouraged and published a modicum of problem-driven research articles. Often, these resulted from extraordinary efforts on their part to craft a special issue out of a regional problem-centered conference or multidisciplinary research project, and occasionally from their desire to publish a particular article that begged for companions, in which case they solicited additional contributions. The grouped articles tended to be interdisciplinary and were sometimes international in scope. We cannot conclude that these articles encouraged more submissions of problem and policy-centric articles, though I have cited a number of good articles (out of what are undoubtedly more in years not examined) that did come over the transom and do offer problem-solving insights. Overall, the IRSR remains a comfortable place for descriptive and causal analyses and for methodological inquiries and extensions.

Current IRSR editor Serge Rey believes that Walter Isard’s aspirations for the journal were reasonable. One way the editors aimed to meet them was by encouraging survey articles on policy, methods, or theory advances, articles that tend to get heavily cited. The IRSR has recently attracted many more European contributions and hopes to attract more on regional development and policy for developing countries. There is, Rey believes, an eager market for problem-driven regional research. The high citation rates in urban development publications for the IRSR’s Special Issue on Smart Growth, coedited by Knapp and Talen (2005), demonstrates this potential in one of the several policy markets.

Of course, there are other traditions, journals, and forums for problem-oriented research in regional science. One reviewer invokes Jim Hite’s Southern Regional Science Association presidential address, in which he argues that:

Southern regional science stands apart … [and] has tended to seek justification for its work not solely within the community of scholars …. but also in the use of the work by pragmatic policy

Certainly, the Southern regionalists from Odum's work on developed quite different conceptions of regional and policies for growth (Odum 1935) than those that defined regional science in its first decades—location theory, input–output, and other methods, a divergence discussed at length in Markusen (1987, 251–55).

Researchers in University business and economic research units, including regional scientists, participate in Association of University Business and Economic Research, which describes itself as “the premier professional organization dedicated to continually improving the quality, effectiveness, and application of research in business, economics, and public policy” (http://www.auber.org/, home page). Also housed at Universities, cooperative extension economic and community development units employ regional scientists who work with state and local governments to develop customized tools and strategies to address local economic problems.

An anonymous reviewer points out that several journals that use the word “policy” in their titles, though only one has “regional science” in its title, and the others are not exclusively populated by regional scientists. These include Growth and Change: A Journal of Urban and Regional Policy, The Economic Development Quarterly (aspiring to effectively bridge “the gap between academics, policy makers, and practitioners”), Journal of Regional Analysis and Policy (formerly Regional Science Perspectives, the journal of the Midwest Regional Science Association), and the Regional Science Association International’s Regional Science Policy and Practice. The latter two are relatively recent, and none would be considered (yet) top-ranked regional science journals.

Perhaps these organizations and journals offer hope for problem-relevant research in regional science. The fact that two of the journals with policy in their titles are newcomers is encouraging and may result from greater pressure on universities and their faculties to provide policy guidance to decision makers and the public. Yet, scholars in planning and public policy schools are responsible for much of the interest in problem-related research (Markusen 2002). Feser (2007) makes the case that public administration and public policy programs may be better equipped to prepare students for kind of research because their curricula emphasize the policy-making process and policy implementation. But faculty in these fields are drawn to their own professional associations (the American Collegiate Schools of Planning and the Association of Public Policy Analysis and Management) and are hard to draw into regional science, especially to the extent that policy research is not given central billing.

Problems and Method in Andrew Isserman’s Scholarship

What about the IRSR’s longest serving editor? Did Andrew Isserman’s research reflect a problem-driven concern or were the methods that he so loved and engaged with dominant in his work?

Isserman made important and often years-consuming contributions to better regional data and methods. He made substantive contributions to population forecasting (Isserman 1977a, 1984; Beaumont and Isserman 1987), including editing a double journal issue on the topic (Isserman 1983), a topic he continued to work on for decades. He improved economic base measurement (Isserman 1977b, 1980; Gerking and Isserman 1981). He developed techniques for estimating missing County Business Patterns data (Isserman and Westervelt, 2006). He tackled the definition of rural, an exercise he argued was important for national policy (Isserman 2002, 2005). In the last few years of his life, he was working with one of his students to develop metrics for rural prosperity. Even in his methods works, however, Isserman did fulfill Isard’s call for more interdisciplinary research. Interestingly, only two of the ten articles just cited were published in the IRSR and just one in the Journal of Regional Science (including Isserman 1977a, 1977b). Three appeared in the Journal of the American Institute of Planners, the flagship planning journal of that time, and others in Socio-Economic Planning Sciences and the Journal of the American Statistical Association. Although Isserman served on its editorial board throughout the 1980s and again in the last decade of his life, he never published in the Journal of Planning Education and Research, though its forerunner, the Bulletin of the Association of Collegiate Schools of Planning ran his “Planning practice and planning education: the case of quantitative methods (1975).”

Isserman often combined his zest for methods with a keen interest in policy questions. A good example is his quasi-experimental work, developed with several students and visiting researchers while Director of the Regional Research Institute at West Virginia University. Isserman and Merrifield (1982) first proposed the use of control group methods in their article for regional science and urban economics, the use of control groups in evaluating regional policy, and subsequently used quasi-experimental methods to study energy boomtowns and growth poles (Isserman and Merrifield 1987). Isserman and Beaumont (1989) further explored quasi-experimental potential.

But Isserman was not content to let his case rest there. In a series of exercises over the decade of the 1990s, he and his colleagues probed whether several important American regional policies had actually achieved their goals, publishing three articles that I have regularly used in my graduate courses. They showed that landing an interstate freeway exchange did significantly increase county prosperity (Rephann and Isserman 1994) and that assets left behind after military base closings sometimes, often slowly, resulted in new growth (Stenberg, Rowley, and Isserman 1994).

The most impressive (and controversial) of these, Isserman and Rephann’s (1995) article showed that average per capita incomes of counties benefiting from the Appalachian Regional Commission’s nearly thirty years of investments were markedly higher than in twin counties around the United States. This finding was important, because the Appalachian Regional Commission’s resources and very existence were at the time threatened with Congressional cuts. It survived, and while pork-barreling may have contributed to that outcome, Isserman’s subsequent work (Isserman 1996, 1997) as the John Whisman Appalachian Scholar (1995–1996) at the Commission helped disseminate his research findings.

Isserman and colleagues’ quasi-experimental research in regional science was path breaking. As Feser (2013, 46) sums up in his review:

Isserman and Merrifield are notable as the first to investigate systematically the strengths and weaknesses of quasi-experimental comparison group designs in regional research settings. Their aim was not just application but also the systematic development of new methods, models, and research procedures. They motivated the value of quasi-experimental research with reference to experimentation as the gold standard in the study of causation and program evaluation.

Feser’s citation analysis (1984–2011 of the Isserman et al. quasi-experimental articles) finds 197 unique documents (104 journal articles, 9 books, 12 book chapters, and 15 theses) referencing one or more of the five core articles, excluding self-citations.

Over the decades, Isserman became more interested in policy and in answering important questions. He seems always to have been willing to serve and at all levels of government. Over time, his participation as an advisor became less methods-driven and more problem-driven. For instance, in the late 1970s and 1980s, he advised the Commerce Department and Census Bureau on population projection. By the 1990s, he was tackling large questions, such as the regional consequences of US immigration policy, a report for the Economic Development Administration that he later published as an Urban Studies article (Isserman 1993b). In the late 1980s and into the 1990s, he led international exchanges with Bulgarian and Soviet academicians on the eve of the dissolution of the Soviet Union. For the latter, he asked his American colleagues to write articles, each from his or her regional expertise, on how the American regional experience might help them face their postcommunist future, articles subsequently published in a special issue of the review. He assigned himself a comprehensive overview of American economic development policy at the state level (Isserman 1994), while I wrote on American regional policy at the federal level (Markusen 1994). In the first decade of this century, now back at University of Illinois and a professor of agricultural and consumer economics as well as of urban and regional planning, he launched once again into new and pressing policy agendas, producing edited volumes on agricultural biotechnology (Isserman 2000) and genetically modified food (Isserman 2001).

In summary, Andrew Isserman in his own research, his field leadership, and his outreach activities did exemplify the vision that Walter Isard laid out for the review. He was both extraordinarily interdisciplinary, publishing widely, and increasingly over his career, dedicated to problem-driven research. He remained an avid methodologist. Over time, he devoted more of his attention and time to untangling thorny issues and working in politically and institutionally complex situations. But instead of picking up a powerful and well-honed tool and looking for a place to apply it, he opened up his mind, educated himself about each issue and its origins, and relied on both reasoning and methods to recommend solutions.

The Challenges to and Fruits of Problem-driven Research

Despite Isserman’s personal commitment to problem-driven research, the IRSR did not attract many problem-driven research articles. Nor have the other regional science journals. Problem-driven research may be more difficult and risky than methods-driven research. It may require mixed methods, those borrowed from other fields, or the creation of new methods. Our principal disciplines—economics, geography—emphasize theory and methods in teaching, not problem solving, though urban and regional planning is an exception.

Both young and experienced researchers may also be responding to incentives within academic and funding institutions. Universities encourage us to publish in highly ranked journals and make substantive contributions to theory or analytical tools, pressures especially strong in formative career stages. Taking time to identify a problem in all its complexity may result in salary and promotion penalties. Funders, such as NSF, do not generally reward problem-driven or policy-relevant research. One can still write policy-relevant articles out of NSF findings, though one’s prospects for future NSF grants are strongly shaped by demonstrating publication in highly ranked journals.

For regional scientists in the academy, working with the problem solvers and policy makers is not generally easy, as the Hirasuna and Hanson special IRSR issue underscores. Policy makers are embedded in institutions that work differently than the academy. Incentives and power structures are different, so that to be successful in influencing policy, one must listen, build relationships, and compromise activities that take time.

Many regional scientists work outside of academia, for nonprofit think tanks or government organizations, where they may have broader opportunities to address problem-based research. Incentives in these settings often present ideological challenges, such as presumption of liberal or conservative norms or restraint of candor when an inquiry or finding may jeopardize some bureaucratic agenda or funding stream. I once interviewed for a Brookings Institution Economic Policy Fellow position with the Ford Administration’s Labor Department where I would be situated in the Secretary’s office. I was asked whether I would be willing to write reports that framed issues such black lung (silicosis) as associated with miners’ choice to work in the industry, thus suggesting that health and safety regulations are not needed. When I returned to Brookings to say I could not accept this placement, they agreed and found me another. Young researchers should be encouraged to take on “real-world” research stints, as my Economics Department Chair had encouraged and given me leave for the Brookings Fellowship, and to consider careers outside academia, but also be mentored to help them cope with the particular culture of the agencies where they work. Professional associations play this role in some fields.

Whether in academia or elsewhere, regional scientists enjoy compensations for pursuing problem-oriented research. For one, problem-driven work may be more fun and intellectually challenging, because it stretches you conceptually, forces you to reach out to other disciplines, and encourages you to learn how to communicate with nonregional scientists. For another, if NSF will not fund you, foundations and even government agencies might, as Isserman’s research record demonstrates. Even if your funded research takes the form of a report or study, you can carve journal articles out of it. Above all, opening up yourself to tough problems is likely to produce, at least occasionally, more stunning findings than safer, incremental investigation. I illustrate these challenges and compensations with cameos of problem-solving research from two eras of research teamwork.

Toward a Better Balance in Regional Science

Andrew Isserman died too soon, before writing a reflective essay on his life’s work that might have included policy impact and personal intellectual history. He did leave us a text of his unfinished Southern Regional Science Association address that described the impact of his work for Department of Housing and Urban Development and the Appalachian Regional Commission (Isserman 2010). He did, in the words of an anonymous reviewer of this article, grow ever more interested in community engagement, learning “how the world works” and “convincing data-drive, imaginative story telling” (quotes from the 2010 article). The reviewer shares that this evolution “at least partly reflects the early influence of Donald McCloskey who was a colleague during his formative years at the University of Iowa in the early 1980s. He (Isserman) frequently mentioned The Rhetoric of Economics (1998) as a compelling book that influenced his research style.”

The dearth of research that is problem-led and policy-relevant is not confined to regional science. As Feser (2007, 1) remarks, “Many of the same factors limiting the engagement of regional scientists in public policy discourse apply to scholars in other fields as well. Indeed, a large literature on the research-policy nexus seeks to understand the reasons why finding from academic science are frequently far removed from the policy arena, even in cases where research is expressly intended to influence public sector decision making.”

How might regional science encourage more problem-solving, policy-oriented research? For one, we could encourage more analysis of policy impact, reflecting on why certain past initiatives have succeeded or failed. We could encourage and put together more problem-driven special issues of regional science journals. We could establish an award in regional science for policy-influential work. In our teaching, we could look back on policy implications and implementation from previous decades of regional science work and ask students to evaluate their impact. In our methods courses, we could reintroduce the historical context and history of thoughts behind each method’s emergence. Feser (2007) offers suggestions for advances in regional science problem-solving and policy fronts. They include curriculum enhancements in regional science for teaching policy process, implementation, and the research–policy nexus, as well as more efforts to network with the policy-making community. One reviewer contents that efforts to reorient should be informed by data and methods recognizable to the discipline and appropriate for the task, citing Brink (2013) as an example. To improve policy-relevant research in agricultural economics, Brink used data from focus group discussions with participants, research consumers, and the policy community.

Certainly, we should use the known data and methods if they fit the problems posed. But regional science should not be confined to current data and methods. We should innovate, including borrowing and improving theories and methods from other fields. New theorizing would be welcome, especially if it brings breakthroughs in understanding human, enterprise, and public sector behavior and the character and practices of regional institutions.

Regional science should be an integrative field. Skilled crafting of problem-related research means looking beyond one’s immediate toolkit and well-known theories. Many problems require institutional knowledge, methods, and/or behavioral or structural theories pioneered in other disciplines. How can we teach our students to feel comfortable venturing onto these broader terrains? For one, we could teach about the formation of and philosophical outlooks of regional science. Economics, my home discipline, long ago shed PhD requirements for history of economic thought and economic history that were in place in the late 1960s and early 1970s, and in my view, is much impoverished as a result. For another, we could require not just an outside field in another discipline but also an advanced survey course in several from among the political science, geography, economics, sociology, policy, and planning fields. Our methods courses could be expanded to include survey research, interviewing, focus groups, field research. And, we could teach our students how to listen to research users, to walk out from under the lamplight, and build our research design around the messy realities of real-world regions.

Regional science is maturing. A first generation has or is nearing retirement. Younger scholars will redefine and change our field. Andy Isserman, a methods advocate and innovator, became more policy oriented over time, placing pressing problems and policy questions at the center of his work and teaching. It would be hard to argue that regional differences have subsided or that there are not effective policies for altering a lagging region’s trajectory or halting corrosive interregional or intra-urban competition. If more of us followed Isserman’s evolutionary path, we could make a difference. In academia, we are privileged to be able to pick our own areas of research. I encourage younger scholars to do problem-driven research, for self-interested as well as public good reasons. I encourage more seasoned researched to become engaged, as a way of testing your ideas and stretching your knowledge base, bringing in funding to support students, and serving the larger regional world.