I've recently finished my PhD (the field almost doesn't matter, but applied mathematics if it helps), and begun a 3 year grant-funded postdoc with a heavy but very flexible research emphasis, in the same general area as my dissertation. At their request, I sent my doctoral adviser (a super senior/recently emeritus professor) a list of the papers I'm currently working on/close to submitting, and my ideas for approximately the next 6 months to a year.

All the papers I'm currently working on represent incremental progress on projects that either developed from my dissertation, or formed as collaborations with others. I didn't outline any wide-eyed ideas, because all the wide-eyed ideas I have will take several years and a long list of incremental progress to come to fruition. In my opinion (formed in part by reading science philosophers like Kuhn), this is how science progresses: incremental progress as long as it yields fruit.

My adviser responded with an alarming level of "concern" (to put it gently) that my current projects are not ambitious enough and he feels they don't match his expectations of me nor do they sufficiently challenge the status quo. I got the impression that he seemed to think that by publishing works that are only a slight improvement on the existing literature, I won't amount to anything, which I took to mean I won't be able to get myself a "real" job once my 3 year postdoc is up.

Oh, and by the way, he suggested a solution, which is essentially to drop everything I'm doing and spend more time working on a particular idea that he thinks will revolutionize a particular area of science. I'm always skeptical any time someone says that, no matter how good the idea, so I pushed back and said no, I'm going to pursue an array of topics, some of which are pretty mainstream, in order to build up a good publication record and good relationships with people in my field.

Ignoring the complexities of funding (my funding is flexible enough to permit me to work on a wide array of sub-topics), am I right to think that an early career academic doesn't really have the political (or emotional!) capital built up to make a "bold move" into an unproven field, which inevitably might involve trying to convince many experts they're doing it wrong? It seems to me like "challenging the status quo" is a dangerous game that can only be played by those with Tenure.

Or do I have it backwards? Is academic science so competitive that one can only progress, career-wise, by challenging the status quo? If so, aren't we just chasing each other around in circles, scientifically speaking?

  • This doesn't answer your question (perhaps subverts it), so I'll leave it as a comment: Perhaps it is okay to do incremental but meaningful work, and even if that means you don't have as "good" of a job in the long term, it might still be worth it. Others in non-academic fields give up on jobs paying much more for quality of life issues. Even if you aren't finding the place where your deep gladness and the world's deep hunger meet you could stand your ground here, especially if other mentors see your work as valuable.
    – kcrisman
    Commented May 24, 2019 at 3:31
  • 2
    if you're in a hot growing area, then you will get a job no matter how incremental your output, as long as you are productive. Betting everything on a revolutionary result is risky then. Conversely if you are in a stagnant field where you and the other hundred graduates this year are waiting for each retirement to have a shot at a job, your research will need to be revolutionary. Commented Jun 2, 2019 at 8:47
  • I wouldn't go so far as to call this an answer, but I for one think it's too risky to bet everything on one high risk/high gain idea, especially if my funding was not directly related to it (I've seen some funding calls specifically for high risk/high gain ideas as well). I think being able to show recent publications from your current postdoc is vital in finding the next position. If you can do it on the side or build up to it and explore it that way, it might be worth it. I am very interested in other answers to this post.
    – penelope
    Commented Jun 3, 2019 at 10:44

2 Answers 2


Consider that he may be correct.

There may not be an upper bound, but there is certainly a lower bound to the 'boldness' of work that will move you to the next level.

Indeed, while progress is usually incremental, few good faculty positions go to individuals that produce 'usual' work. Your senior advisor has certainly had time to feel out what is likely to succeed.

  • I'll admit the existence of a lower bound, but just because a new approach is bold doesn't mean it will necessarily pan out. In this particular case I have scientific reasons to believe that this new approach won't necessarily yield the promised revolution. I'll admit that most faculty positions must require research uniqueness (we can't give this job to anyone else, because only you do this), but I seem wary of the idea that research uniqueness is only found by jumping off a cliff.
    – icurays1
    Commented May 24, 2019 at 0:55
  • just because a new approach is bold doesn't mean it will necessarily pan out — Exactly right. But if you know in advance that something will out, it isn’t really research; it’s just homework. Good faculty positions (and research grants) don’t go to people who only do homework.
    – JeffE
    Commented May 24, 2019 at 20:17

Rather sounds like a rhetoric question to me seeing the competition on positions with tenure.

And this is not restricted to the post-doc phase. I have worked in groups where the professor already and intentionally choosed research questions/methods with high risk of success/failure of the individual PhD student. Different professors will have very different research/risk/diversification strategies. Some groups work with same amount of people on one topic, other on 3 or 4.

If you have funding for 3 years, which is over average for post-docs, I think it is clear you are expected to deliver something significant, not only incremental. Results that would allow to acquire further funding.

Also, I don't have the same understanding of philosophy of science (Kuhn) as you. Paradigms are not shaken by incremental research, general relativity etc. were revolutionary theories that were adapted slowly and incrementally by the community. It's fun to read about this. There is even a stackexchange site (history of science)

Another view is, do you win scientific prizes with incremental research? Most of them go to researchers that developed new concepts/measurement methods/theories. Of course incremental research has to be done and most of the tenured researchers and PhD students work most of the time on such projects. But the post-docs, in my opinion, are really the one selected to risk something and being able to manage to accomplish it. And you can also find that a nobel prize on average gets awarded on average over 20 years after the discovery and it is known most of the researcher, depending on field, make significant discoveries in their 20-30s, PhD and post-doc phase again.

In the best case you already acquire funding during your post-doc time and can hire PhD students on your own as PI. Then you can diversify your research topics from risky to incremental

I don't think it would be a wise decision, to follow his advise 100% and drop all your current topics you are experienced in. From his overall strategy this can make sense to put single researcher on very risky new topics, I know such professors myself. In the aftermath, if it succeeded and you got outstanding results, you and he did everything right, if not it is very likely you regret it to not have proceeded with projects you were experienced and successful in. I would suggest to negotiate again with him how you diversify the research projects and how division of labour is organized with PhD students.


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