Career advice from Richard Thaler

My advice for young researchers at the start of their career is… Work on your own ideas, not your advisor’s ideas (or at least in addition to her ideas). And spend more time thinking and less time reading. Too much reading leads people to think of small variations on existing studies. Admittedly my strategy of writing the paper first and only then reading the literature (or, more likely, letting the referees tell me what they think I should have read) is an extreme one, but it is better than trying to read everything. Try writing the first paper on some topic, not the tenth, and never the 50th.

Here is the rest of the interview.


Shorter Thaler- be creative and original, dammit!

Good advice! But in most fields, most people shouldn't follow strategies that work for the top 1% of the field.

We live in Lake Wobegone.

I've been wondering about that, and I'm not sure it's true.
My adviser's advice was to "catch the big fish and then move on". I've seen other researchers who keep hammering at the same problem (to continue the metaphor, they harvest the fish to extinction). The question is, is there a synergy between the "idea people" and the "workhorses" who collect a ton of data to flesh out theories that other people develop and produce incremental advances. I don't have an answer, but I can imagine a world where everyone is really trying to push the limits, rather than doing derivative work. Maybe there wouldn't be as many publications, but in some fields (e.g. biology) that would be a blessing because we are drowning in boring or poorly thought out experiments.

In other words, too many people try to use high quantity to compensate for low quality (and originality).

Perhaps he should recognise that some people (me!) are just not as bright as he is: plodders plod.

This is seriously a recipe for wasting a year repeating someone else's work.

The reason you read the literature is to find out what hasn't been done, so you know that's where you should put your efforts.

Plus, what Millian said.

So true. Didn't a guest on Russ Roberts program comment that on average one year more reading is required these days by PhDs due to the Great Stagnation? That said, both the Special Theory of Relativity and the General Theory of Relativity were suggested prior to Einstein, so Einstein did well not to review the literature, as he would have been discouraged to pontificate (unless you think his wife in fact derived these equations, as some do). Google Lorentz Transform and see this:

In order to think outside the box, you first have to know what's in it. That takes reading. Lots of it.

Your average PhD student probably reads too much of the literature (a form of procrastination), so Thaler's advice (in moderation) is sound.

However, I disagree with his advice to write the first paper (not the 10th or 50th) on a topic. A PhD student or new assistant professor has no credibility, and I believe if he or she wrote the first paper on a topic, they would be unable to publish it anywhere good. (Think of George Akerlof's, or Black-Scholes', struggles.) But between the 2nd and 10th paper is probably optimal. Also known as the research frontier.

I'm not familiar with Black-Scholes' struggles, but I would say that it's probably a good thing that Black-Scholes didn't follow your advice. Maybe, it's different in economics, but I would say that if you have a well known advisor as a (second) co-author, your paper will be taken seriously by plenty of readers. Again, I don't know whether it's common in economics to have a grad student as first author and his or her advisor as second. In my field in engineering, that's the norm.

The 2nd through 10th paper are fine, provided that the 1st through 9th papers' authors seem to you to have taken completely the wrong approach. My modification of Thaler's advice would be to first try to read the seminal paper on a topic. If there is a seminal paper, find a different topic. And, the order is to think of a topic/problem, then look for the paper/solution, not the other way around.

Regarding Millian's comment on the top 1%, I think that this advice works for the top 10%. Most people, whether inside the top 10% or out, will eventually find a way to graduate, regardless of which advice they follow, i.e., they would eventually give up on Thaler's strategy if it didn't work for them. It would be a shame, however, if one was in the top 10% (or 1%) and did not realize one's potential because one followed a strategy that was fine for the average, but not for the top 10% (or 1%).

The purpose of grad school is to get out.

It's funny to me that people claim "you get to work on your own ideas" as a benefit when (1) it's not really true and (2) people contradict it immediately.

If pleasing your advisor gets you done faster, then you get to do your own thing, then do that.

Definitely disagree. The purpose of grad school is to develop a professional and publication record for the next step of your career, whether in academia or industry. In my opinion, the worst thing one can do is graduate before one has established a strong record only to find out that one can't get a "normal" PhD job and, at the same time, is "overqualified" for jobs that don't require PhDs. Late 20s is way too soon to rise to the level of one's incompetence.

The purpose of grad school is to write a dissertation. Everything else is secondary.

Economics PhD's face a very low unemployment rate.

Few students in economics publish much, outside of the top few departments, so your comment is not very relevant. To economics anyway.

Every field is a little different, I almost agree with BC on engineering but many of these things are self-correcting. If you find yourself in an awesome situation with an awesome advisor, hell, stay forever. Such people don't really need advice, though.

You economists are living the salad days, I suspect ("Hey, grad student, just create a new field!"), so enjoy them.

Hardly anyone graduates with a publication record coming out of economics and if they do, then it's almost certainly true that the quantity to quality ratio of that record is astronomically high. In which case see Thalers anecdote by tversky on the guy who publishes his waste basket. At least in applied micro fields, tenure cases are oftentimes six publications in top field/ general interest mix.

Grad school is a time to get a phd in economics and prepare yourself to get a job in which you will be successful and happy.

@BC: Your first and second sentences are a non sequitur. Black and Scholes were both young researchers, so the advisor issue is irrelevant. As an academic in *economics*, I know that PhD students are expected to produce a dissertation that is their own work, and it is common for their first papers to be written solo -- it is a bad signal, often, to co-author with your advisor. Means you cannot fly with your own wings. **Economics is not engineering.** Thus, I repeat: a newbie claiming to invente a new area of research is not credible. If as a newly minted PhD I write a paper called ''Economics and Neuroscience'', people will laugh at me (figuratively).

I also disagree with your second paragraph. A single paper will not begin and end an entire topic. The first paper proposes a first pass at the problem that provides a useful solution. The second improves (does not mean the first was wrong), the third improves on the second, etc. At some point, improvement is negligible (Thaler's point I think). Most economics PhDs should therefore try to find a topic that has just started, so they can contribute something important, and still be taken seriously (since they did not start the literature).

I agree, however, that it's unwise to aim to just ''get out'' as soon as possible, if you want a good job, academic or otherwise. In economics, publications before PhD graduation are neither expected nor necessary, but you want to polish your dissertation to the point where it will be ready for submission to journals your first year in the tenure track (and of course, it will sell better during job market interviews).

This is kind of like two people arguing over whether Godfather 1 is better than Godfather 2.

Everyone is different. Some people can only be successful if they follow Thalers advice, and some can only be successful if they become like the straw man professor he's criticizing. Clearly, Thaler is a deeply creative person whose productivity is directly tied to working in a wide open space. Others thrive in the same way by working in an almost congested area.

Assistant professors have to figure out their own production function and then start the grind full force in that direction. Most of us will be in the 99% by definition but there are nonetheless a lot of people who think that what works for them will work for everyone and that is not true. I think you know hearing Thaler whether you are of the same species as him with regards to basic personality and productivity. It doesn't mean you're a genius that you do your best work by that kind of creativity. It doesn't mean anything except that that is how you work, and Thalers point IMO is that you should carefully discern which type of worker you are. If you try to mimic someone who is fundamentally cut from a different cloth, you will likely fail.

+1 You can only work with whatever endowment you have and it is better to be a productive plodder than to try to be say Tirole or Black or Merton and wind up being unproductive. Figure out what works for you and then do it!

I was advised to read one paper a day. Sometimes I read more (over the course of a month), sometimes I read less. It's very easy for a biologist to spend all their time collecting data. Researchers need to take a step back, and reading good papers is a way to do that.

Wonderful, now advisors don't even provide ideas.

Just remember:

This is advice of a Prof with


Wanna play the lottery of writing before researching?

This is probably good advice for anyone in the field of history.

Two of the most influential historians of the 20th Century, Pirenne and Braudel, both wrote their seminal texts from the confines of German prisons in the First and Second World Wars, respectively. Their time away from their libraries and notes forced them to reflect on their research in terms of grand themes instead of being bogged down by the minutiae. Although once they were released they both updated their manuscripts with the benefit of the available literature, they essentially "wrote the paper first."

I'm largely with Thaler on this one. Start with an idea. Flesh it out in skeleton form. Then consult the literature to see where it fits, modifying as necessary. It's quite possible you've re-invented the wheel; then you must decide whether you like this topic enough to extend the literature, or move on to something new. As you get older, some papers will develop from inception as extensions of the literature because you'll know certain literatures intimately by then. But ideas first, literature second, but if it turns out there is a literature, your paper should read as if you knew it all along.

Eh, maybe. The risk is the project may not seem to referees to be anything more than a review of the existing literature. This might not be all bad. Sometimes review articles are publishable and someone might even compliment you for producing a "brilliant synthesis." But you're not likely to reroute the discipline that way (whatever the discipline may be) .

Have had the experience of writing the first paper on a topic that no one else would touch before being published in a minor journal after a decade. Only to find that the second paper that cited me gets more citations for their refinements and that subsequent papers get into journals that rejected my first paper for being outside of the field, I can only say: Thaler's advice works if you're good at winning the lottery.

I basically agree with Thaler on this one, and he's being only a bit more blunt than advice I have heard from others. As one example to support his case...I was presenting my research on the spending response to fiscal stimulus at an economic conference (think summer camp for economists but indoors). I was still on my warm up slides, one explaining mental accounting via a quote when the organizer barked out: "Next slide! I don't care what Dick Thaler thinks!" (Or maybe it was something a touch more colorful?) His point, of course, was skip the lit review and get to *your contribution.* I was mildly comforted when he made the next presenter skip several slides, because I do try to be brief on other people's stuff (on my advisor's and in this case co-author's advice). Nonetheless, I would have been skewered if I walked in there and acted like I was the first person to imagine something like mental accounting. To make a contribution you need to produce new and valued insights...Thaler is right that most young researchers can get stuck in consumer of knowledge stage (reading) and need a huge 'nudge' to become a producer of knowledge (writing). Of course, that path depends on your field of study, personal disposition, and pure luck.

Thaler is being too cute ... a young researcher has two options, one low-risk, the other high-risk. The low-risk option is join an existing conversation by publishing a paper that makes some minor or incremental contribution to one's field. The high-risk option is to try to start a new conversation, like Thaler suggests in his interview.

Also, I have to say that Kahneman and Tversky are way over-rated; prospect theory is a joke

This advice sounds nice, but speaking as somebody who has gone through it, the academy is interested only in evolutionary ideas, not revolutionary ones. Most journals and reviewers only want to see tiny incremental augmentations to previously published work, mostly because they can't trust themselves to recognize whether truly original thinking on something is genius or insanity.

There is nothing radical or cute about Thaler's advice: "spend more time thinking and less time reading." Of course, it's not easy to find a novel angle, but if you aren't making some contribution to the body of knowledge (incremental or even destructive is fine) then you probably shouldn't be doing research...there are plenty of other (better paid) things for economists to do.

But the most prestigious journals (Nature and Science) want revolutionary ideas. This is despite the fact that they cannot distinguish genius from insanity (or inanity).

I appreciate the advice for career. As young people, we have creativity and originality that veterans lack. We should make full use of all of our talent and make our career a great start.

I can't comment on Economics, but as a one-time grad student in Genetics I always assumed that the Golden Rule applied, He who had the gold (my advisor) made the rules, and suggested the research topics.

The same is true for physics (and really, grant-supported science or engineering fields in general, in the US). The originality comes in doing something noteworthy that one's advisor can discuss in their reports to the funding agency and that you and the advisor can publish.

In short, you pick your advisor, not your topic.

My suggestion is to read widely and choose a few papers that you found very exciting, but examined different topics. Figure out how they are connected.

Admittedly my strategy of writing the paper first and only then reading the literature (or, more likely, letting the referees tell me what they think I should have read) is an extreme one, but it is better than trying to read everything.

As a referee I find this attitude very presumptuous.

I got my PhD in physics. Graduate students can barely read the literature, let alone come up with their own ideas.

Isn't it the great point of pride of Paul Krugman and the whole economics profession that nobody has read the literature, and they are damn well are not going to start now?

Paul Krugman often brags about his refusal to read any economics written before the time he began grad school, and that includes even Bertil Ohlin on the economics of nternational trade:

Paul Krugman, Oct. 1999: "Let me begin with an embarrassing admission: until I began working on this chapter, I had never actually read Ohlin's IInterregional and International Trade."

I agree. To suceed in career it is not sufficient to have read many books, but it is necessary to have thought a lot.

Gilberto Salgado, whose dissertation Mike Munger called "brilliant", once told me how he was forced to spend months without reading because of a medical condition -- and so he spent much of that time thinking about economic problems. And it was during this time that he came up with his thesis, which included contributions to the work of Israel Kirzner, who was present at his defense and acknowledged Salgado's insights. Salgado himself assured me that he would not have come up with these ideas had he spent most of his time reading.

Here is Munger's flattering comment on Salgado: "There is no moral sense that attaches to a mistaken or wrong action, however. The idea of error, and its implications, are explored in a brilliant but little-known doctoral thesis by Gilberto Salgado [“The Economics of Entrepreneurial Error”] (1999)."

Here is a book that cites a lot of Salgado's Kirznerean analysis:

The world needs a lot of tinkerers, but only a few visionaries. Therefore the world needs a lot more people reading a heavy volume and figuring out an incremental improvement. There's less demand for a deep thinker that flings forth fully formed ideas from his brows derived from first principles and his own genius.

Though admittedly if you are a genius, your comparative advantage may be in the latter. The problem is of course that due to our personal biases 35 out of 10 of geniuses realize their brilliance.

For example there's no question that the half-baked BS spewing out of Nassim Taleb could do with a healthy dose of appraisal of previous literature, and personal modesty about the power of one's owns original ideas.

Scholars who struggle would do well to pick up an instrument and try to write a song. The art of creating music is not much different than that of writing prose. You can only write a song as complex as your training. But, what is the limit of your training? Setting aside the physical abilities required to, say, play Beethoven or Mendelssohn on the piano, actually conceptualizing one's own original work as complex - regardless of one's ability to play the piano - is what is most important. Conceptualizing a complex piece could require no more of the greatest genius than his or her listening to eithers' piano sonatas. This is why it can be said that anyone can contribute - it just takes imagination.

But, as others have suggested, this is the lottery idea to scholarly production. Imagining special relativity without ever having studied physics prior would seem to be more of a mental game than a productive activity. We must engage the conversations - know them intimately - in order to contribute something to them. It is nigh on impossible to do something great for intellectual advancement if we limit our ideas to the simple notion that we simply sit awhile and try to conjure a great idea without ever having engaged the debate.

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