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I am half way thorough my second year as a posdoc and I have a reasonable production (4 published papers in good journals and two other under review). I also have several ongoing/potential research projects and I am finding it hard to figure out how to manage my time and energy regarding them.

Here is the problem: among these projects, there are some that are fairly secure in terms of publication, meaning that I feel confident that within reasonable time and with reasonable effort those projects will lead to papers published in good journals (let us simplify assuming that "good" means Q1). However, these are not particularly motivating problems/proposals (for me). The main issue is their lack of motivation, mathematically in particular and scientifically in general. It is not that they are not good problems at all, or uninteresting in their entirety, they just don't seem to have an underlying mathematical or scientific question to them.

On the other hand, there is a handful of potential projects that I find motivating, some of them proposed to me by other mathematicians (tenured professors with solid careers) and some of them my own, but whose perspective of success is much less clear. These are interesting questions and/or research directions but there is no certainty that I will be able to get something out of them. And on top of that, they require an important time investment.

I am tempted to follow a strategy based on working on the "publishable" projects just the amount of time required to move forward with them and dedicate the rest of the time to the other projects, but I would appreciate points of view, comments or suggestions on the matter.

I could not find a question to which I would say that this is a duplicate, although I do think that these issues ought to be common for people at my stage of the career.

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    I don't understand how a problem that "doesn't seem to have an underlying mathematical or scientific question to it" might still be good or (from the perspective of science) interesting. Can you clarify? Oct 26, 2020 at 7:40
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    I didn't write "interesting", I wrote that they are "fairly secure in terms of publication".
    – hamath
    Oct 26, 2020 at 11:52
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    I was referring to this specific sentence: "It is not that they are not good problems at all, or uninteresting in their entirety, they just don't seem to have an underlying mathematical or scientific question to them." That doesn't add up for me. Oct 26, 2020 at 12:22
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    Maybe the word "hard" is missing in this sentence, as in "a hard underlying mathematical/scientific question". Then it would make sense. Easier stuff is easier to get done and thus easier to get published. Oct 26, 2020 at 12:24
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    Well, I don't think that something is either interesting or it isn't. A paper may have nice application or an interesting approach, fill up a gap in the theory and many other features that make it somehow interesting without having a deeper scientific or mathematical aim to it. As for your second comment, I believe that hardness and interest are not correlated, at least not reciprocally: although really deep, really interesting questions are often hard to answer, there are plenty of difficult but uninteresting problems floating around in math.
    – hamath
    Oct 26, 2020 at 12:31

4 Answers 4

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I guess my advice would be, first, to get a permanent position, say on the tenure path and then get tenure. Do what you need to do to set a baseline.

Second, there is no reason why you need to make a final decision now and never review it. In the short term you could (probably should) work on stuff that gets you to tenure primarily, filling in with ideas on more interesting topics. Then, as the world becomes more secure you can morph into a situation that seems more satisfying.

Just keep notebooks of ideas as you go along, so that when you think of something "interesting" that might be pursued, you don't lose track of it later.

Stay flexible. Establish a base. Then move on.

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    Quoting for wikipedia on Brower <<"After completing his dissertation, Brouwer made a conscious decision to temporarily keep his contentious ideas under wraps and to concentrate on demonstrating his mathematical prowess" (Davis (2000), p. 95); by 1910 he had published a number of important papers, in particular the Fixed Point Theorem. Hilbert (...) helped him receive a regular academic appointment (1912) at the University of Amsterdam (Davis, p. 96). It was then that "Brouwer felt free to return to his revolutionary project which he was now calling intuitionism " (ibid). >> Oct 25, 2020 at 22:52
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    @AlecosPapadopoulos, this is a wonderful quotation/point. Would you please make it an "answer", rather than a "comment", so that it will persist more robustly? Thanks, best wishes, ... Oct 25, 2020 at 23:13
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    “Stay flexible. Establish a base. Then move on.” This seems like an excellent synthesis of the advice, and it’s much appreciated! I probably have to learn to take the anxiety down a notch and realize that there’s time to do all sort of things in the way of a career.
    – hamath
    Oct 26, 2020 at 0:52
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    Completely agree with you. But equally depressed about the realistic necessity to do so. Oct 26, 2020 at 8:11
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At the suggestion of @paulgarrett, what Wikipedia narrates for Luitzen Egbertus Jan Brouwer provides a historical aura (to say the least...) to the sensible advise of user @Buffy:

<<...Brouwer then "embarked on a self-righteous campaign to reconstruct mathematical practice from the ground up so as to satisfy his philosophical convictions"; indeed his thesis advisor refused to accept his Chapter II "as it stands, ... all interwoven with some kind of pessimism and mystical attitude to life which is not mathematics, nor has anything to do with the foundations of mathematics" (Davis, p. 94 quoting van Stigt, p. 41). Nevertheless, in 1908:

"... Brouwer, in a paper entitled 'The untrustworthiness of the principles of logic', challenged the belief that the rules of the classical logic, which have come down to us essentially from Aristotle (384--322 B.C.) have an absolute validity, independent of the subject matter to which they are applied" (Kleene (1952), p. 46).

"After completing his dissertation, Brouwer made a conscious decision to temporarily keep his contentious ideas under wraps and to concentrate on demonstrating his mathematical prowess" (Davis (2000), p. 95); by 1910 he had published a number of important papers, in particular the Fixed Point Theorem. Hilbert—the formalist with whom the intuitionist Brouwer would ultimately spend years in conflict—admired the young man and helped him receive a regular academic appointment (1912) at the University of Amsterdam (Davis, p. 96). It was then that "Brouwer felt free to return to his revolutionary project which he was now calling intuitionism " (ibid). >>

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Personally I have always gone for what I was motivated to do, and in that way I think I built up a rather unique view and understanding of things that later served me well achieving some top publications. I was wondering for quite some time whether my publication record is good enough, but now I know my publication record is quite strong (although it wasn't for some time), so it paid off. I should say that it was clear to me from pretty early that although many researchers are stronger than me in many respects, I am original, and I was always motivated to follow my own agenda. The good thing about this regarding publications is that I never had any worry (and rightly so, although of course I didn't have any guarantee) that somebody else will achieve the same thing and get it published before me, because even if somebody else would approach the same problem, chances are my take would be different enough (actually once I and a "competing" group came out with major work on the same problem at the same time but our solutions were so different without being directly contradicting that we could co-exist peacefully). Not sure whether this could be a problem with your "secure publications"; I know some worry about this, and good ideas of some were in fact published by somebody else shortly before they could finish.

That said, I'm not sure whether I should recommend this approach to others. One reason is that I grew up in a "slow" environment without much pressure, and was given enough time (6 years plus 2 abroad) to build something up before actually having to compete for a permanent position. In a different system my approach may not have worked. Another reason is that I had some confidence in my originality as well as exit strategies in place in case this wouldn't have worked out. I was basically prepared to leave rather than adapting in case I couldn't do my work how I wanted to do it. I have always tried to be realistic. I wouldn't just blindly trust that it works, I would have some ideas in case it wouldn't. And to be honest, maybe I was a bit lucky with the people I met and the positions I got, and it could've gone wrong.

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  • Interesting. Thanks for that.
    – Buffy
    Oct 25, 2020 at 21:59
  • Thanks for your reply. I guess our contexts are rather different, but I do feel inspired by your confidence in your own work, methods and ideas; it’s important not to follow the trends just because they are... trendy. Sometimes scientists can be curiously conservative in regards to what paths of research should be followed and having an agenda of one’s own (and being confident about it) is a great asset
    – hamath
    Oct 26, 2020 at 0:49
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    I think the major issue here is that many people focus too much on career and what they are "expected to do" to the extent that they don't realise that another approach can also work. Whenever somebody told me "this-or-that is required for the career", I always asked myself, do I really believe this, and can it be done differently? But then it's true that doing whatever we want will not normally secure a career, so I had to keep my eyes open and do at least some things that are seen as "required" - I picked those that were most fun and fit best into my "personal agenda". Oct 26, 2020 at 14:54
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Hedge your bets. See the topics you work on as an investment portfolio. You certainly don't want to put everything into something risky, but to have a shot at making it big, you might want to take one or two more speculative investments with your time. So dedicate some time to the grander, motivating topics.

Think also about the time-scales: you'll probably want to have a mixture of short- and long-term investments. For example, some papers I make I know won't be overnight successes. There just aren't enough other people working directly on those topics for me to see that much activity related to my work that soon. But I'm confident that over time they'll be read and cited.

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  • Thanks for the reply; it sort of combines nicely with the one from @Buffy.
    – hamath
    Oct 26, 2020 at 12:17

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