In response to my last essay at this web site, “On Becoming an Environmental Economist,” several readers suggested that someday I should write about the origins of my various research initiatives over the past 25 years. Today, I’m doing that sooner than anyone might have expected!
This is feasible because — also quite recently — I was asked by my colleague, Hannah Riley Bowles, the instructor in the Harvard Kennedy School’s Doctoral Research Seminar, to make a presentation to the first-year students in the Ph.D. program in public policy on how research programs develop. To prepare for this, I reflected on my research projects over the past 25 years since receiving my PhD in economics at Harvard and joining the Kennedy School faculty, and as I began to write some notes for my presentation, a flow chart of research origins, subjects, and products started to emerge. You can view my PowerPoint presentation (you need to use Slide Show mode to see the animation) here.
In this essay, I describe the elements of that flow chart of research sources, topics, and selected publications (and provide some screen shots of the PowerPoint deck).
As will probably be apparent, I found the process of preparing for Professor Bowles’s seminar valuable, because it forced me – for the first time in 25 years – to step back and reflect systematically on the origins of my research projects and the connections among them. So, I recommend this process to other researchers, as I think you may find it rewarding. And, for would-be researchers, that is, PhD students, I hope the results below will be informative.
An Ex Post Exploration of How Research Programs Develop
In carrying out this ex post exploration of how research programs may develop, I identified eleven types of sources of research ideas and projects. In approximate chronological order (but not necessarily in order of importance), these are:
- Involvement with the Policy World
- Picking Up on Someone Else’s Work
- Student Interest
- Responding to Others’ Work
- Class Assignment
I begin with how my dissertation research subsequently led to several avenues of further research and writing.
Dissertation — Analyzing Land Use
My 1988 Ph.D. thesis examined econometrically the factors that had led to the dramatic depletion of forested wetlands in the southern United States over the previous five decades. Before commenting on how my dissertation stimulated my subsequent research, I should acknowledge that my dissertation topic itself grew of out of some consulting work I was doing at the time for the Environmental Defense Fund, in particular an analysis for James T. B. Tripp of how U.S. Army Corps of Engineers flood control projects were providing economic incentives for landowners to convert their forested wetlands to agricultural croplands.
My dissertation led directly to a pair of journal articles published in 1990 in the American Economic Review (with Adam Jaffe) and the Journal of Environmental Economics and Management. But more striking – given the theme of this essay – is that several years later I realized that the general econometric approach and simulation model could be applied to a very different question, namely, analyzing the anticipated costs of biological carbon sequestration as a means of reducing net concentrations of carbon dioxide (CO2) in the atmosphere, linked with global climate change. That recognition led to another article in the American Economic Review (1999), and then to a series of other, related projects on carbon sequestration (with Richard Newell 2000, and with Ruben Lubowski and Andrew Plantinga 2006, both in the Journal of Environmental Economics and Management), as well as a broader research initiative on factors affecting land-use decisions (with Plantinga and Lubowski in the Journal of Urban Economics in 2002 and Land Economics in 2008). More recent work with Andrew Plantinga and Robin Cross (that does not appear in the schematic below) has involved an econometric analysis of the concept and reality of “terroir” associated with the production of premium wines (American Economic Review 2011, Journal of Wine Economics 2011).
A Less Direct Legacy of Dissertation: Economics of Technological Change
A fundamental aspect of the econometric modeling involved in some of the land-use models above, including my dissertation research, was the estimation of the parameters of an empirical distribution of some heterogeneous attribute of land parcels, such as potential crop revenue (due to varying land quality, for example). As costs of production fall, for example, that distribution would be swept, with various parcels going into production at various points in time. Adam Jaffe and I hoped that this same sort of model could be applied to the process of technological diffusion, that is, the process of gradual adoption of some new technology over time.
As it turned out, however, the model was less useful than we first thought it would be for analyzing the factors affecting technology diffusion, and so we abandoned it for that purpose. But this led us to explore other conceptual and empirical approaches to assessing the factors that lead to the diffusion of environmental technologies. We developed a new framework for comparing empirically the effects of alternative environmental policy instruments on the diffusion of new technology, including Pigouvian taxes, technology adoption subsidies, and technology standards, with an empirical application to the diffusion of thermal insulation in new home construction, comparing the effects of energy prices, insulation cost, and building codes (Journal of Environmental Economics and Management 1995). Related work with Nolan Miller and Lori (Snyder) Bennear followed in 2003 (American Economic Review).
Given our interest in the diffusion (adoption) of energy-efficiency technologies, it was natural to think about exploring the factors that affect the innovation (commercialization) of such technologies. A very different model was developed — with Richard Newell taking the lead as part of his Harvard dissertation research — and an empirical application was made to analyzing the innovation of specific household energy-consuming durable goods (such as water heaters and air conditioners). This work appeared in the Quarterly Journal of Economics in 1999.
More broadly, our interest in the innovation and diffusion energy efficiency technologies led us to explore in a series of articles the so-called “energy paradox” of apparently slow diffusion of technologies that appear to pay for themselves, as well as other issues related to energy-efficiency technological change (Energy Journal 1994, Resource and Energy Economics 1994, Energy Policy 1994, Elsevier Handbook of Economics 2003, Ecological Economics 2005, Energy Economics 2006, and many others). And, recently, with a resurgence of interest in the energy paradox in the context of global climate change, Richard Newell and I have launched a new research initiative, with support from the Alfred P. Sloan Foundation.
Because I’ve sought to describe the origins of my research somewhat chronologically, I began with my dissertation research. The fact that several strands of research — some directly related and some indirectly related to my dissertation — subsequently emerged will surely not surprise academic readers of this essay. However, a considerably greater influence (indeed, the most important influence) on my research portfolio has come from my involvement — not with fellow scholars — but with practitioners in the world of public policy. That may come as a surprise to some readers, and it is to this illustration of the two-way street between research and practice to which I now turn.
Involvement with the Policy World
A phone call I received in the late spring of 1988 — a week before my Harvard graduation — from Senator Timothy Wirth (D-Colorado), and a meeting shortly thereafter in Washington with Senator Wirth and his long-time friend and colleague, Senator John Heinz (R-Pennsylvania) led to an agreement that I would direct for them a study intended to inform the Presidential debates on environmental policy in that election year — Project 88: Harnessing Market Forces to Protect the Environment (and a follow-up study in 1991, Project 88 — Round II, Incentives for Action: Designing Market-Based Environmental Strategies).
Many pages could be written — and, indeed, many have been written — about the influence that Project 88, sponsored by Senators Wirth and Heinz, subsequently had on policy developments at the federal level in Washington (including the path-breaking SO2 allowance trading program in the 1990 Clean Air Act amendments), within many states, and internationally in locations ranging from the European Union to China. But my purpose in this essay is to examine the origins of my research portfolio, and so I will turn instead to reflect on the ways my experience with Project 88 (and related policy engagements with the White House, the Congress, and others) stimulated new paths of my scholarly research.
One path of research activity soon focused on normative analysis of alternative policy instruments, including work on: transaction costs in cap-and-trade markets (Journal of Environmental Economics and Management 1995), the effects of correlated uncertainty on the choice between price and quantity instruments (Journal of Environmental Economics and Management 1996), vintage-differentiated regulations (Stanford Environmental Law Journal 2006), and policy instruments in second-best settings (with Lori Bennear, Environmental and Resource Economics 2007). [The work on correlated uncertainty also illustrates an example of another source of research ideas, namely picking up on research by someone else, because this work was directly inspired by a footnote in Professor Martin Weitzman‘s classic work on “Prices vs. Quantities” (Review of Economic Studies 1974).]
Another area of work on normative analysis of policy instruments focused broadly on market-based instruments (with Robert Hahn, American Economic Review 1992; with Richard Newell, Journal of Regulatory Economics 2003; and the Elsevier Handbook of Environmental Economics 2003). Other work focused more specifically on cap-and-trade systems (Journal of Economic Perspectives 1998; with Robert Hahn, Journal of Law and Economics 2011; and with Richard Schmalensee, Journal of Economic Perspectives 2013).
A conceptually distinct path of research that also found its origins in my work on Project 88 has involved examinations of the positive political economy of environmental policy (with Robert Hahn, Ecology Law Quarterly 1991; with Nathaniel Keohane and Richard Revesz, Harvard Environmental Law Review 1998; with Robert Hahn and Sheila Olmstead, Harvard Environmental Law Review 2003).
Even this extensive set of research projects and publications that derive from my work on Project 88 — depicted in the figure above — understates the influence that my work on Project 88 with Senators Wirth and Heinz has had on my scholarly research over the years. This is because much of my work on global climate change policy, for example, has in fact focused on the potential use of market-based instruments in that realm, but for purposes of this essay, I associate that later work on climate policy with two other origins, namely, conferences and funders.
Conferences and Funders
Gradually over the 25 years since receipt of my PhD, my research has evolved from diverse work across environmental and natural resources economics, to more and more focus each year on various aspects of global climate change and related public policies.
“Climate skeptics” and other opponents of action to address climate change have sometimes accused the research community of focusing on climate change because “that is where the money is.” Although there are sound reasons for focusing on climate change other than the availability of funds (such as the importance of the problem, and the methodological challenges it poses), there is some partial truth to the accusation. Indeed, numerous national governments and major philanthropic foundations have made it their goal to stimulate research (and action) on climate change.
One part of my work in this realm has been research on national and sub-national climate policy instruments, often focused on the design of market-based instruments, including but not limited to cap-and-trade mechanisms (Brookings Institution 2007; Harvard Environmental Law Review 2008; Oxford Review of Economic Policy 2008; and my work on the Intergovernmental Panel on Climate Change, Second, 1995, and Third, 2001, and Fifth Assessment Reports.
An invitation from the Doris Duke Charitable Foundation to propose and eventually direct an international research and outreach project on international climate policy architecture led to much (but not all) of my work on international climate policy cooperation (with Joseph Aldy and Scott Barrett, Climate Policy 2003; with Scott Barrett, International Environmental Agreements 2003: with Sheila Olmstead, American Economic Review 2006; three books with Joseph Aldy published by Cambridge University Press 2007, 2009, 2010; an article with Judson Jaffe and Matthew Ranson, Ecology Law Quarterly 2010; and ongoing work on the IPCC Fifth Assessment Report 2010-2014; and much more).
Many professors who are reading this essay will not be the least bit surprised to learn that another origin of research ideas has been interest expressed by graduate students. Three important examples stand out in my case.
One I have already written about above. When Richard Newell (my very first PhD student) came to Harvard for graduate school in 1993, he brought with him an abiding interest in the relationship between science, technology, and policy. At the time, Adam Jaffe and I were continuing our work on the diffusion of energy-efficiency technologies, and then the U.S. Department of Energy (DOE) solicited proposals for research that could improve the modeling of technological change in integrated assessment models of climate change (so this covers two other origins — involvement with the policy world, and potential funding). All of this came together in a joint research initiative, funded by DOE, which supported Newell’s dissertation research on factors affecting the pace and direction of energy-efficiency technology innovation. This led to a subsequent publication with Jaffe and Newell (Quarterly Journal of Economics 1999), as well as series of other collaborations with Newell, which are on-going to this day.
In 1999, Sheila (Cavanagh) Olmstead came to the Harvard PhD program in public policy with a strong background and keen interests in water resources and water policy. I brought on board Michael Hanemann, then a professor at the University of California at Berkeley, as a collaborator, and together we applied (successfully) to the National Science Foundation for a grant that supported Sheila’s dissertation research on econometrically estimating demand for municipal water in the presence of block-rate pricing schedules. Not only did that lead directly to some published work (with Olmstead and Hanemann, Journal of Environmental Economics and Management 2007), but led indirectly to other research on water pricing(with Olmstead, Water Resources Research 2009).
The work on carbon sequestration and land use described above with Ruben Lubowski and Andrew Plantinga (Journal of Environmental Economics and Management 2006; Journal of Urban Economics 2002; Land Economics 2008) also deserves mention in this part of the essay, because it all grew out of Ruben Lubowski‘s PhD dissertation research at Harvard.
Responding to Others’ Work
I mentioned above an example of picking up on someone else’s work (in a positive sense), namely a footnote in Marty Weitzman’s classic 1974 article on “Prices vs Quantities” in which he noted that he was assuming statistical independence between marginal benefits and marginal costs, which stimulated me to relax that assumption and pursue the analysis (which led to my article on the effects of correlated uncertainty in 1996 in the Journal of Environmental Economics and Management).
By contrast, sometimes researchers can be stimulated to do work in order to question others’ previous work (and related conventional wisdom). This was the case with my collaborative work examining the topic of “corporate social responsibility,” an area of scholarship that some colleagues and I believed was populated by research and writing that generated more heat than light. A conference we organized at Harvard led to a subsequent book that examined Environmental Protection and the Social Responsibility of Firms: Perspectives from Law, Economics, and Business (with Harvard Law School professor, Bruce Hay, and Harvard Business School professor, Richard Vietor, 2005). Later, I took the next step with a follow-up article with Vietor and his Harvard Business School colleague, Forest Reinhardt (Review of Environmental Economics and Policy 2008), and another with Reinhardt (Oxford Review of Economic Policy 2010).
Classroom teaching can itself provide inspiration for research. In 2002, I was teaching a small “reading and research course” for PhD students interested in environmental economics, and lamented one day that the increasingly popular concept of “sustainability” seemed to lack a clear definition or interpretation that made sense in economic terms. I offered a possible economic interpretation in class, and within a week, two students — Gernot Wagner and Alexander Wagner (unrelated) — had written out a mathematically formalized version of my interpretation. We collaborated on writing a brief article that provided background as well as further exploration (Economic Letters 2003).
It may (or may not) come as a surprise that consulting (work I do outside of my Harvard responsibilities, sometimes for compensation, sometimes not) can also lead to interesting research ideas. In my case, this has led to my thinking more carefully — with collaborators — about the analytical methods that surround net present value analysis (also called, benefit-cost analysis).
This has led to a series of papers on various dimensions of net present value analysis in the environmental realm, including such topics as: the meaning, limits, and value of the Kaldor-Hicks criterion (with Kenneth Arrow and others, Science 1996); the role of discounting (with Lawrence Goulder, Nature 2002); new benefit-estimation methods (with Paul Portney, Journal of Risk and Uncertainty 1994; and with Lori Bennear and Alexander Wagner, Journal of Regulatory Economics 2005); and the use of Monte Carlo analysis to incorporate uncertainty in regulatory impact analysis (with Judson Jaffe, Regulation and Governance 2007).
Many of my PhD students over the years have written term papers for courses that led to manuscript that were eventually published in academic journals. But in my own case, because my PhD training in economics at Harvard did not include any courses in environmental economics (none existed at the time, as you may have noted in my previous essay, “On Becoming an Environmental Economist”), the only example I can provide of this origin of research is in a different area, namely economic history. This is an area in which I took two wonderful courses from Professor Jeffrey Williamson (about which I wrote in my previous post). An econometric analysis I carried out for one of those courses — “A Model of English Demographic Change: 1573-1873” was subsequently published (Explorations in Economic History 1988).
Invitations (and other origins)
There’s a clear positive correlation between the onset of grey hair and the frequency of invitations to write articles (or books) for publication. These have included: an article with Don Fullerton on how economists view the environment in Nature (1998); an article on common property resources in the American Economic Review (2011); my ongoing column, “An Economic Perspective” in The Environmental Forum (2006-present); my blog, “An Economic View of the Environment,” which was launched in 2009; two books of my collected works, 1988-1999 and 2000-2011 (Edward Elgar 2001, 2013); and three editions of a book of selected readings in environmental economics (W. W. Norton 2000, 2005, 2012).
Results of an Ex Post Exploration of Research Origins
Putting all of that together in a single flow chart results in the figure below, which is much clearer in a PDF version. You can also view the entire PowerPoint presentation (you need to use Slide Show mode to see the animation) here.
As I said at the outset, I found the process of preparing this slide deck for Professor Bowles’s seminar valuable, because it enabled me to step back and reflect systematically on the origins of my research initiatives over the years and the relationships among them. I recommend this process to other academics, because I believe it can be rewarding. And, for academics in-the-making, that is, PhD students, I hope this essay may be informative.