Monday, January 30, 2006

Quality versus Quantity

A graduate student asks
Is it better to have a large number of good papers or a small number of great papers?
The answer is both, great papers to show you have depth and many good papers to show that the great papers were not flukes.

But suppose Fate gives you two roads and you had to choose. History will only remember your best work, so you'll want great papers or the world will eventually forget you. But a CV with many solid good papers will sell better and should help you land better jobs and grants. You'll be perceived as an expert in the field based more on breadth more than depth.

Underlying the question is whether a graduate student should take aim at very hard questions hoping for an award-winning paper. Unless you have some specific new approach that might work or you can still get reasonable results even if the big problem does not fall, you should try to focus more on tractable problems that will build up your research reputation.


  1. "But a CV with many solid good papers will sell better and should help you land better jobs and grants."

    Really?? I would have thought that one Turing-award-winning result would get you tenure anywhere on the planet, even if you had nothing else on your CV.

    Then again, that approach didn't work for Steve Cook, did it? Hmm.

  2. One risk is to spend time fruitlessly trying to prove a great result, the other is to spend time writing up minuscule results for obscure conferences. How can the graduate student take his own measure? By working on problems which are within his reach, but at the limit of his ability. That's also a good way (the only way?) for the student to make progress and further develop his abilities.

  3. Judging what to work on always entails risk; our judgements of the difficulty of problems are not always reliable.

    One solution is to diversify as one would an investment portfolio: invest some in high risk (longer term) and some in lower risk (shorter term).

    This strategy suggests that you have at least a couple of different things to work on that are of differing levels of risk.

  4. you should always push yourself, especially in graduate school. so it makes sense that your number of 2nd-tier publications (like soda, ccc, socg) should be at most double your number of 1st-tier publications (like focs, stoc), as an example, otherwise maybe you're not fulfilling your potential.

    (of course this scales to 2nd vs. 3rd vs. 4th tier, etc.)

  5. Jeff, correct me if I'm wrong, but didn't Cook publish his NP-completeness paper while at the University of Toronto (that is, after failing to get tenure at Berkeley)?

  6. ''2nd-tier publications (like soda, ccc, socg) should be at most double your number of 1st-tier publications (like focs, stoc)''

    I think your definition of 2nd-tier conferences versus 1st-tier conferences esp. about soda and socg are quite wrong.

  7. I agree with the last anonymous. Moreover, one should not only care about the publication venue but also about the impact of the concrete paper . Sometimes papers from the 3rd tier conferences get a lot of attention... since they are good.

  8. We do not always know how to distinguish a great paper from a merely very good one. Only the perspective of history allow us to do so. Best-paper awwards are very poor predictors of future great papers.

  9. Don't waste too much time obsessing about the mythological total ordering on results, conferences, and theoreticians that so many get wound up about. It's like they're doing this to prove they are the smartest kids in a world-wide advanced maths class, and not for the advancement of knowledge...

    You should be able to identify the contribution of each project you are involved with, and be able to explain its relevance to somebody who is not a theoretician, or at least, a theoretician not in your immediate circle of the like-minded. Never appeal to aesthetics, unless you are simplifying an important result with a complicated proof, or unifying some apparently unrelated results. Do not claim that a problem has practical consequences without being able to convincingly explain these consequences to a practitioner who would supposedly benefit.

    You also need to be able to distinguish between a long term plan that will likely have a pay-off and a time-sink. Good rules of thumb are the generation of publons at fixed time intervals, or to do round-robin scheduling until a project seems on the brink of success, at which point you go for that project.

    Breadth and depth are both important. Depth for showing that you can do outstanding work and be a leader, and breadth for demonstrating you are flexible. Breadth work will also help you maintain a large frontier of possible problems to work on in the future, it will help you converse with more people about technical matters, it will help you put things in perspective, and it could be very useful if your first career path (say, tenure track theoretician at top 20 university) does not pan out.

    As long as you keep working on a variety of problems with the knowledge and taste recognize the ones that matter and the honesty and self-awareness to know when you are not getting anywhere, you should do fine work.

  10. One should not hope for getting good results early in his research careeer just because he/she isnt exposed to the vast ocean. I as a grad student personally feel that the paper should have some quality but to expect a paper which can fetch you Turing award is beyond the reach of many grad students, not to undermine their capabilities.