Mike Weisbach is writing an excellentbook 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!
