The Economist’s Craft

An Introduction to Research, Publishing, and Professional Development

Michael S. Weisbach

• Publisher: Princeton University Press
• Year: 2021
• Print ISBN: 9780691216485, 9780691216492
• eBook ISBN: 9780691216584
• Topic: Economía
• Subtopic: Teoría económica

An incisive guide that helps up-and-coming economists become successful scholars

The Economist's Craft introduces graduate students and rising scholars to the essentials of research, writing, and other critical skills for a successful career in economics. Michael Weisbach enables you to become more effective at communicating your ideas, emphasizing the importance of choosing topics that will have a lasting impact. He explains how to write clearly and compellingly, present and publish your findings, navigate the job market, and more.

Walking readers through each stage of a research project, Weisbach demonstrates how to develop research around a theme so that the value from a body of work is more than the sum of its individual papers. He discusses how to structure each section of an academic article and describes the steps that follow the completion of an initial draft, from presenting and revising to circulating and eventually publishing. Weisbach reveals how to get the most out of graduate school, how the journal review process works, how universities decide promotions and tenure, and how to manage your career and continue to seek out rewarding new opportunities.

A how-to guide for the aspiring economist, The Economist's Craft covers a host of important issues rarely taught in the graduate classroom, providing readers with the tools and insights they need to succeed as professional scholars.

1

Introduction—How Academic Research Gets Done

WHEN WE THINK about the way in which we do academic research, we might think of the mathematician Andrew Wiles, who won the Abel Prize in 2016 for proving Fermat’s Last Theorem. This “theorem” was originally stated by Pierre de Fermat in the seventeenth century, although Fermat did not provide a proof.¹ For over three hundred years, no one could prove that Fermat’s Last Theorem was true, nor provide a counterexample to show it was false. Fermat’s Last Theorem would baffle many of the world’s greatest mathematicians—including Leonhard Euler and David Hilbert, each of whom spent several years attempting to solve it—and it became one of the greatest unsolved problems in mathematics, or really in any field. A German industrialist and amateur mathematician who himself had tried and failed to solve the problem established the Wolfskehl Prize at the end of the nineteenth century—a substantial financial reward to be given to the scholar who solved the problem. A century later, Wiles, who was a professor at Princeton at the time, worked on proving Fermat’s Last Theorem in total secrecy for a number of years, letting only his wife know that he was working on the problem. One can only imagine what the conversations were like at lunch when his colleagues or students asked Wiles about his research. When Wiles finally announced the solution in 1993, it was generally considered one of the greatest mathematical discoveries of all time.

Those of us who become academic researchers in any field look to Wiles’s discovery as the “Holy Grail” of what we would like to achieve with our scholarship. We all would love to solve a famous problem that was formulated by someone else, especially one that many others have unsuccessfully attempted to solve. Such an accomplishment would represent a substantial contribution to knowledge, and the scholar who solved the problem would become an “academic celebrity.” Many of us get our PhD with the dream of making a discovery like Wiles’s and gaining a similar kind of acclaim.

However, the actual experience of the vast majority of researchers, even the most successful ones, is nothing like Wiles’s. Not only are most researchers far less successful than Wiles, but the approach they take to research is very different. Indeed, what is relevant to most researchers about Wiles’s remarkable discovery is that it illustrates what most research is not. There are important differences between his experience and the approach most of us have to take to become successful researchers. At least three such differences are worth highlighting.

First, most problems we solve were not stated by someone else, and certainly not three hundred years ago by someone as famous as Fermat. Most of the time, at least half of the battle is coming up with the right questions to ask and the right way to ask them. In fact, once a question is asked, answering it is often quite straightforward. In 1937, Ronald Coase asked a question no one had asked before: “What determines the boundaries of the firm?” His paper asking this question led to the development of the field of organizational economics. Coase earned the 1991 Nobel Prize in Economics in large part because he had the foresight to be the first person to ask such an important question. Coase also proposed reasons for the boundaries of firms, but his explanation was fairly straightforward. Once the question was asked, many people would have come to the same conclusion he did. The brilliant part of Coase’s paper was the asking, not the answering.²

Second, unlike Wiles’s experience, research in most fields is intensely collaborative. In the sciences, research is usually centered on a laboratory or a research group working together on related problems. In the social sciences, the collaboration tends to be less structured but is no less important. Most papers are coauthored, and even sole-authored papers go through many rounds of revision based on discussions with colleagues before they are published. In most fields, it is very rare for someone working alone in secret to come up with an important discovery.

Third, the discussion following Wiles’s discovery was about whether his proof was in fact correct, since there was no question about the importance of the problem he was trying to solve. However, the discussion about most academic papers usually centers on the nature of the contribution, the questions the paper asks, and the limitations of the analysis. Frequently the most important question in an academic seminar, and the one for which the author most often does not have a good answer, is “Why do we care about this paper?”

The burden of any researcher is to explain why the question she is asking is important and why she did what she did to answer it.³ Most importantly, she should explain why the results tell us something we want to know, or should want to know, about the world around us. The ability of a researcher to provide such explanations can, and often does, determine the success of a particular research project. A paper that fails to explain why its contribution is important will have trouble getting published, and even if it does get published, it will have little impact. Sometimes a researcher lacks an adequate explanation because the paper does not tell us anything particularly important. But often a researcher lacks a good explanation because she failed to “put her best foot forward” in explaining to a reader why he should care about the paper’s results.

When I was a doctoral student, I was the beneficiary of the spectacularly good training provided by the MIT Economics Department. In my classes, I learned how to solve models, derive properties of estimators, and critique other people’s work, as well as many other useful skills. What I did not learn in class was how actually to do research. That I learned by going to the National Bureau of Economic Research (NBER) office in Cambridge, Massachusetts, every evening, where I hung out with some of the best faculty and doctoral students from both Harvard and MIT. We spent hours and hours talking about what was good research and what was not, what we thought were the important questions yet to be solved, and whether the seminar presentation we heard that day made any sense. We also read each other’s papers carefully and helped one another become successful scholars.

One thing I have observed over the years is that most graduate programs tend to prepare students for problems like the one Andrew Wiles solved, not the ones they are much more likely to deal with in their future careers. Traditional classes in graduate programs teach students to solve problems that have been posed for them, which is what they have to do to pass their qualifying exams. Solving a well-known question is what Wiles did when he solved Fermat’s Last Theorem, although the challenge, of course, was on a totally different scale than passing a qualifying exam.

Where many graduate programs struggle is by not providing young researchers with the experiences and insights that are necessary to be successful researchers. They do not, for the most part, teach students the craft of being a scholar. In particular, they do not teach students how to pick research projects that will have lasting impact, how to communicate why a project will be important, how to handle data properly, how to write up results in an appropriately scientific yet readable manner, and how to interpret results in a way that others will find reasonable. Most scholars learn these skills as doctoral students in an apprenticeship-type relationship with their thesis adviser, from other faculty, and from fellow students.

Young scholars often ask my advice on various aspects of the research process. Their questions tend to arise from the craft rather than the science of economics. Young scholars want to know how they should pick research topics, find coauthors, write readable and interesting prose (in English), structure academic papers, present and interpret results, and cite other scholars. Most frequently, they have questions about all aspects of the publication process. In addition, academics of all ages do not think enough about their own professional development and do not invest in the human capital that would allow them to enjoy their jobs throughout their career.

Learning the economist’s craft—how to do research and how to proceed in career development—has historically been a random, word-of-mouth process. Some scholars are fortunate enough to have someone to teach them the craft of the profession, while others go their entire career without figuring it out. There is no reason why something this important must be communicated in a haphazard manner by word of mouth. It can and should be written down.

The State of Academic Research

Before getting into the particulars of how to do research, it is important to understand the market in which we work and how it has affected research. While basic research in some fields is done by the corporate and government sectors, in most fields it tends to be dominated by universities. Universities reward faculty in large part based on their research, so faculty have substantial incentives to do research and publish their findings in the most prestigious outlets possible.

The academic marketplace can be summarized by three main trends: First, there has been substantial growth in academic research globally. Many universities, both in the United States and, especially, in other countries, have decided that they should improve their research reputation and are strongly encouraging their faculty to become more active scholars. Second, this growth has led to more competition among faculty for research ideas. This competition, in combination with the maturing of most fields of study, has led faculty to become increasingly specialized. Third, the growth in the number of top-level journals has not matched that of research-active faculty, so it has become increasingly difficult to publish a paper in a “top-tier” journal.

THE GROWTH IN ACADEMIC RESEARCH

Many universities have cut back on the number of their tenure-track faculty as a way of saving money, but others are trying to gain prestige by increasing their research presence. In the thirty-plus years since I left graduate school in 1987, the number of universities expecting their faculty to publish in top outlets has increased dramatically. While my PhD is from an economics department, I have focused my research on financial economics, a subfield of economics that is mostly taught in business schools. I have observed a number of changes in the structure of finance academia since I left graduate school. Similar changes have occurred in economics departments and also in related fields such as accounting.

In 1987, little research was published in the top journals that came from outside the top twenty or twenty-five US departments. Now there are probably at least one hundred US departments that require publication in top journals as a condition of earning tenure. Internationally, the growth in this expectation has been even larger. In 1987, only two European finance departments consistently produced top finance research, London Business School and INSEAD. Today there are probably at least ten or fifteen departments with as many active researchers as London Business School and INSEAD had in 1987. In Asia, little serious finance research was going on in 1987. Now there are at least three very good departments in Singapore and four or five in both Hong Kong and Seoul. In mainland China, academic research activity has grown so much that it is virtually impossible to keep track of all the good departments unless you live there.

Growth in doctoral programs has mirrored the increase in high-quality departments. In the 1980s and 1990s, with rare exceptions, most of the best finance PhD students graduated from the top ten US departments. Now the best students on the academic job market come from all over the world. European departments regularly place students at the top five US departments, and US departments ranked outside the top fifteen or twenty regularly produce extremely good students who land jobs at top departments. Students from Asian programs are getting better every year, and it is only a matter of time before, like their European counterparts, they are regularly placing at the top of the market. As a result of this growth in doctoral programs, there are many more active researchers in the world today than when I began my career, and that number is growing at an accelerating rate.

SPECIALIZATION IN RESEARCH

What about the problems that are being studied? In most fields, contributions tend to become narrower and narrower over time as researchers become increasingly specialized. The basic questions in any field remain the same, so researchers discover the most fundamental contributions first, then refine them over time.

Occasionally, there is a seminal event, research breakthrough, or technological innovation that spurs new research. In my field, one such event was the Financial Crisis of 2008. While catastrophic for the world economy, the crisis led to an important burst of research seeking to understand its causes, the effect of new financial products on the economy and how they should be regulated, potential government interventions during a financial crisis, whether banks should be allowed to be “too big to fail,” and similar issues.

Recently, the availability of immense amounts of data and the computing tools to work with such data have revolutionized many fields. Much recent research in many fields of economics has been based on newly available large databases, dramatically increased computing speed, and new approaches to data analysis, such as machine learning. These developments have pushed economics and related fields toward applied empirical work. Roger Backhouse and Béatrice Cherrier point out that ten of the previous twelve winners of the John Bates Clark Award, which is given to the top American economist under age forty, focus on empirical or applied work.⁴ This pattern is in marked contrast to the early years of the award, when it most often recognized work in theoretical economic...

Table of contents

• Cover
• Front matter
• Series Page
• Title Page
• Copyright
• Dedication
• Contents
• Preface
• 1 Introduction—How Academic Research Gets Done
• Part I. Selecting a Topic
• Part II. Writing a Draft
• Part III. Once a Draft is Complete: Presentations, Distribution, and Publication
• Part IV. Being a Successful Academic
• Epilogue—Academic Success beyond the PhD
• Bibliography
• Index