Thursday, April 16, 2020

Weisbach advice

Mike Weisbach is writing an excellent book of advice, A Field Guide to Economics: A Young Scholar’s Introduction to Research, Publishing, and Professional Development. As a good scholar he is circulating the manuscript. It's really half advice and half a meditation on how the profession works and how it should work.

There is a lot of good advice, and a lot of good questions. I'll highlight a few things I disagree with, but don't take that as criticism of the project, rather an invitation to read and think about the issues yourself.

Mike advises throughout that you have to spend time explaining why your research is important. I don't have the experience of reading papers that I understand easily but that under-sell their importance. My experience is the exact opposite. I am nearly always lost halfway through any seminar, and notice we seldom get to the actual contribution before 1:00. Bloviation about how something is important before I know what it is annoys me. I struggle with most papers to figure out what it is the authors have actually done, usually explained badly or not at all in the introduction. So I offer contrary advice: don't bury the lede. Tell us what you have done, first and foremost. in the simplest possible terms. Then we can figure out why it's important, how it contributes to a literature, and so on.

I noted quite a few famous -- even Nobel-Prize winning -- papers in which the authors had no idea why it was important. Mike counters with a few examples from corporate finance that really needed some effort. It's a worthy discussion. I've also noticed it's a cultural thing -- corporate finance seems to want a long discussion of why it's important before we know what it is, asset pricing and macro seem a bit more the other way. Though, perhaps I'm getting old, but the tendency to puff up papers seems to be increasing.

Here too, perhaps I am confusing positive and normative advice. I wish people wrote more transparent papers. But Mike is trying to tell you how to get ahead in the profession, and lots of people do that very well by writing papers that I find hard to read!

I encouraged Mike to have a longer discussion of what not to do. Much writing and self-improvement consists of editing, recognizing simple mistakes and fixing them. "Write clearly" is hard to follow. "Don't tell us why it's important before we know what it is" is easier to follow. I think the next draft will have more of that.

Mike start well with "how to pick a topic." He encourages young researchers to pick a research program. It is important to emerge with a program, a brand name, a set of ideas that you are known for. But by his own admission that's not how Mike worked. It's certainly not how I have worked. Every time I sit down to write what I think will be a Nobel-prize winning masterpiece it falls flat. When I think I'm going to make a clever point and move on, it results in a well-cited paper and a program.

Mike encourages you to ask big questions. I think questions are a dime a dozen. Research topics are about a hunch of an answer. Unraveling DNA did not happen by researchers asking "how can we cure cancer." It happened from a fascination with X-ray crystallography. Modern physics -- Galileo, Newton -- was not born from "how do we start an industrial revolution and cure world poverty?" It started by trying to explain the motion of the stars.

Here's a good question for topic selection. Should you address politically controversial issues? Should you follow the topic of the day? COVID-19 papers are being produced at amazing speed, just as financial crisis papers were for 10 years. There is an interesting tradeoff of salience vs. permanence. But it is also a fact, emphasized by Mike, that research advances are produced collaboratively, by a group of people working on similar topics, and that much success is measured by influence, by others following in your footsteps. The lone sage answering a question from a mountaintop tends to be unproductive and ignored.

Mike's general career advice is also a bit how to be like Mike -- a successful tenured academic at a strong university with an active and well respected post-tenure portfolio of academic research. His examples tend to be our academic superstars. Here my advice was more positive and less normative. There are lots of careers doing research, and many paths to success. Applied research in think tanks, government, central banks, NGOs, is an important and valuable social contribution even if it doesn't get published in Econometrica. The career paths of Larry Summers, Thomas Piketty, Paul Krugman, Ben Bernanke, are as worthy of study as those of Gene Fama and  Bob Lucas. How to avoid the post-tenure slump many people experience who focus on academic publication is worthy of study too.

But these are small notes, and I hope they encourage you to read Mike's book and think for yourself what advice is good for younger scholars, or for you if you are one.

The main advice I usually give is "don't listen to old people like me, you figure it out." Especially on topics, none of my heroes did what the old people of their generation told them to do!


  1. John, Thanks so much for writing this blog entry! Obviously we don't agree on everything. But if we did, life would be pretty boring. I tried to write down what I have been telling students for years. One thing I also tell them is to talk with others since my way doesn't work for everyone.

    The remainder of the book will cover some of the topics John mentioned, such as how a young academic plans her career with a goal of exploring some of the options discussed above.

    If any readers of the Grumpy Economist have a chance to look at the manuscript and have reactions, please let me know what they are.

    Thanks again!

    Mike W

    PS. Blog readers will be interested in knowing that John sent me 17 pages of suggestions the other day, which goes well beyond what anyone can reasonably expect to receive! Perhaps John is as bored as the rest of us stuck at home all day??

  2. The advice I got long ago: find an interesting problem and solve it.

    I was working on a little research project I thought was going to be amazing! Trying to correlate frequency and density of digital social interactions (emails, board posts) on a learning management system and the grades people earned. Results? Only accounted for 4% of the variance. Hardly mind blowing. The data set severely violated homoskedasticity - but, something interesting did pop up: for people who typed under 10k characters in a semester the distribution was very wide. But, past 10k characters, the variation was still normal, but a higher floor for the minimum grade earned - no one below 65% whereas under 10K, the minimum grade was a 0% At one point I had a dummy variable in there and it accounted for 67% of the variance. But the dummy variable wasn't a good one because of the way it was constructed and the assumptions behind the classification.

    Anyway, short story how research can surprise you and show you how wrong you were! Ha.


  3. I haven't read the manuscript but I couldn't agree more with your take on the need to say "why your findings are important". Having read countless papers and sat through too many 90 minute seminars to count or remember, the pain associated with having someone drone on and and on about why their paper is more important or new relative to everything that came before is so often unbearable. And let's be totally honest, when you read a paper how often do you just skip the intro and flip to the substance so you can "see what the hell they are doing"? Hmm?

    But this is, of course, where research economics is as a profession. The journal system is broken. Has been for 20 years or more. As you have previously written, the blogosphere is supplanting the journals because they are calcified relics of the past that only serve to gate academia and don't provide researchers with access to new and emerging research.

    Just yesterday I was reading about new COVID studies appearing in JAMA and elsewhere that are being used to inform COVID research underway TODAY. Can you imagine that occurring at JF or AER or Ecta? Me neither. The journals don't exist to disseminate ideas to those producing other new ideas. They exist to confer long-lived rents to the academy. Down with journal and long live the blogosphere!

    1. I hear you, but economies and economic data availability both move considerably more slowly than viruses, so "immediate" research is neither as necessary nor as possible in economics as it is in medicine. The quality variance of those JAMA articles is also *very* high.

      Bottom line: there's room for both blogs and journals. One isn't a substitute for the other.

  4. One "rule of thumb" I learned at U Chicago (I'm thinking it was from Stigler) was that your research will remain relevant for approximately as long as the age of the articles in your footnotes. (Reference articles written in 2010, you'll be read until about 2030). It doesn't hurt to know / reference some of the classic debates from the literature.


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