This may be a little off topic. But as new Ph.D in geometry/topology area, I have a feeling that it is relatively harder to publish a descent paper. However after seeing some peers who study PDE or Geometric analysis have a lot of paper, like 5-6 papers when graduate and after 3 years posdoc, they will had around 12-15papers, and also have relatively higher citation on mathscinet, I am a little depressed. Even some professors in some good university (rank 50+) can have such publication when admitted as an AP in the geometry/topology area. So should I publish some 'small' results to catch up peers during the beginning of my career or bet on Bigger results, which may not succeed within 1 or 2 years. (sometimes I found the knowledge got from graduate school is far away from enough, or a new tool need to be studied in order to understand something new, this study could take times).

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    $\begingroup$ Although not directly tied to publication number, Terry Tao's post on extending one's range seems relevant: terrytao.wordpress.com/career-advice/…. Of course, knowing one's range in the first place requires a realistic appraisal of one's strength. Publishing a number of papers on "small" results could help establish a baseline for this. $\endgroup$ – Jon Bannon Oct 17 '12 at 19:59

(I wanted to write more than the comments allowed, so I marked this as community wiki so that I don't feel guilty about getting reputation for it).

Here is the advice I give to postdocs when they are trying to figure out what projects to work on and what publication rate is appropriate for their goals.

  1. People tend to judge you based on some combination of your best work and your total paper counts. The better the mathematician, the more they will judge you by your best work as opposed to number of papers. So it is better to write a few strong papers than lots of mediocre papers.

  2. However, it's much better to write mediocre papers than to not write strong papers! In other words, you need to be aware that people are going to judge you based on what you produce during your postdoc. If you are doing a standard 3 year postdoc, then you will be applying for jobs during your third year, so you have exactly two years in which to prove yourself. You need to have things to show for those two years!

  3. The upshot of the above is that you should have a mixture of long-term and short-term projects, but during your postdoc you should concentrate the majority (though not all) your attention on projects that you can realistically complete before you go on the job market. And you should also work on multiple projects at once rather than concentrating all your attention on one goal (which might or might not pan out).

  4. As far as figuring out how productive you need to be, I advise you to do the following. Make a list of people who are in your field (different fields have different rates of publication) and who have gotten tenure-track jobs at places you aspire to be at in the last 5-10 years. Next, go to their webpages and look at their CV's. You want to have a publication record (both in terms of number of papers and in terms of quality of journals) after your postdoc which is similar to them when they were on the tenure-track job market. If you are way off, then you might want to reconsider your career goals.

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    $\begingroup$ This is all good advice, but #4 can be tricky. One reason is that it's hard to reconstruct what someone's job application might have looked like, because of issues like how far before publication they were circulating preprints. However, there are deeper ambiguities in comparing CVs. You'll often see a case where X had twice as many papers as Y in roughly comparable journals. Were Y's papers judged more impressive by experts? Was Y just lucky? Did X face a tougher year on the job market? Did X solve a two-body problem by turning down more prestigious offers? You generally won't know. $\endgroup$ – Henry Cohn Oct 17 '12 at 20:49
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    $\begingroup$ I agree that it is hard to make precise comparisons. However, it gives you a rough idea of what is needed. In my experience talking to postdocs, lots of them are totally clueless about what the CV's of job candidates at (say) top 50 schools look like. Moreover, faculty are often somewhat clueless and loathe to deliver bad news. Another good source of recent info is the math jobs rumor wiki. It is very educational to look at the cv's of people on the various short lists (with the understanding that many of those lists are wrong). $\endgroup$ – Andy Putman Oct 17 '12 at 21:01
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    $\begingroup$ Definitely, it's better to gather this information (while keeping in mind that there's a lot of noise). $\endgroup$ – Henry Cohn Oct 17 '12 at 21:07
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    $\begingroup$ Just a thought: it's often hard to judge the strength of your own results. Often while writing a dissertation, one has a lot of ideas that they can't fit in or don't have time to work on but which seem easy because he/she has developed a big machine. These seem less easy to people who have not written that same dissertation. I recommend to recent Ph.D.'s that they turn those ideas into papers. Chances are that they are going to make lots of mistakes in trying to publish their results and may have a turnaround as long as a year on papers. So it's worth writing some small papers early on. $\endgroup$ – Eric Katz Oct 18 '12 at 3:15
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    $\begingroup$ Following on from Eric's comment, I wish more 'big machines' would get published as such. You can write a longish paper in two parts: part one sets up the machine, and part two spits out a whole bunch of results with minimal extra effort. It doesn't matter if the payoff results individually have shorter proofs that bypass the machine - you're just demonstrating what the machine can do in order to sell it to the mathematical community. If they buy it, they'll streamline it and use it to prove their own results, and suddenly your work is the centre of attention. $\endgroup$ – Colin Reid Oct 18 '12 at 3:40

The question you ask, I think is fair and good, and I wish you to find the right answer. Probably the question is in the mind of many young researchers, although the answer should be individual, I think it is relevant for MO. But actually I am not in good position to give advises on your main question,

so let me comment on the following " ...bet on Bigger results, which may not succeed..."

I do not think it is good to "bet on Big results", I mean you may try to invest your time to studying some big conjecture or modern popular technique, but when one is young it is difficult (imho) to estimate properly ratio (efforts spent/result obtained).

The way which I choose for myself (actually much later when I got PhD) is the following: I start working on the subject when:

a) I am 100% sure that I will get "some" (may be "bad") result, which can be obtained in reasonable amount of time - say 2-3 months

b) I hope for some "big result" if I would be lucky/clever/whatever. I mean I see some "big problem", such that 100% guaranteed result is some "partial case" of it.

To the best of knowledge similar way is used by many people.


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