March 6, 2010
1. Work at several problems at a time. If you only work on one problem and get stuck, you might get depressed. It is nice to have an easier back-up problem. The back-up problem will work as an anti-depressant and will allow you to go back to your difficult problem in a better mood. John told me that for him the best approach is to juggle six problems at a time.
2. Pick your problems with specific goals in mind. The problems you work on shouldn’t be picked at random. They should balance each other. Here is the list of projects he suggests you have:
- Big problem. One problem should be both difficult and important. It should be your personal equivalent to the Riemann hypothesis. It is not wise to put all your time into such a problem. It most probably will make you depressed without making you successful. But it is nice to get back to your big problem from time to time. What if you do stumble on a productive idea? That may lead you to become famous without having sacrificed everything.
- Workable problem. You should have one problem where it’s clear what to do. It’s best if this problem requires a lot of tedious work. As soon as you get stuck on other problems, you can go back to this problem and move forward on the next steps. This will revive your sense of accomplishment. It is great to have a problem around that can be advanced when you do not feel creative or when you are tired.
- Book problem. Consider the book you are working on as one of your problems. If you’re always writing a book, you’ll write many of them. If you’re not in the mood to be writing prose, then work on math problems that will be in your book.
- Fun problem. Life is hardly worth living if you are not having fun. You should always have at least one problem that you do for fun.
3. Enjoy your life. Important problems should never interfere with having fun.
This advice from J.H. Conway is excerpted from the blog post of Tanya Khovanova
January 6, 2010
1. Raise your quality standards as high as you can live with, avoid wasting your time on routine problems, and always try to work as closely as possible at the boundary of your abilities. Do this, because it is the only way of discovering how that boundary should be moved forward.
2. We all like our work to be socially relevant and scientifically sound. If we can find a topic satisfying both desires, we are lucky; if the two targets are in conflict with each other, let the requirement of scientific soundness prevail.
3. Never tackle a problem of which you can be pretty sure that (now or in the near future) it will be tackled by others who are, in relation to that problem, at least as competent and well-equipped as you.
The original text of the rules together with the author’s comments can be found here (HTML) or here (PDF).
November 12, 2009
A list by Dmitry Podolsky
Update: another such list (this time of 24 problems) by Sean Carroll, the three most important open problems in physics by the Nobel Prize winner Vitaly Ginzburg, and a more extensive list (see also the updated book version of this list) by the same author.
May 24, 2009
This very interesting and very controversial issue is discussed here, here and here. The discussion was triggered by this post at the YFS blog on the all not-too-nice kinds of people one encounters in science and on losing one’s illusions down the road into the academe (see also here for a related post at the RS blog); for a kind of alternative point of view see here.
May 9, 2009
Choosing a research problem to work on is a tough decision to make, and the relevant advice is rather scarce.
So far I have found only a handful of reasonably looking tips:
- work on important problems (R. Hamming, You and Your Research)
- go for the messes, i.e., for the areas far from being crystal clear
(S. Weinberg, Scientist: Four golden lessons)
- look for an unoccupied niche that has potential (this and some other good tips can be found in the paper Picking a research problem — the critical decision which is primarily addressed to the researchers in biology and medicine but can be of interest to the other scientists too)
- keep several (if possible, not too closely related) problems of varying difficulty to work on, so that you can switch to another problem when you get stuck (for more on this see e.g. here)
- try to move beyond the subject of your Ph.D. thesis (if you have already defended one, indeed) or your postdoc (or your postdoctoral mentor, for that matter); more broadly, beyond your current area of research (see e.g. this post of Terence Tao). This has an extra benefit of reducing the risk of being scooped as discussed here.
- regularly attend the conferences and join (or run) a seminar and/or a journal club: the talks can be an important source of inspiration
- do something you will enjoy doing and what you feel you can do
- your work should rather open the way to new breakthroughs than close the whole subject down
The last three tips are somewhat of a common wisdom and can be found in a number of places; see e.g. the article Choosing a research topic by Richard Reis, which contains some further interesting thoughts on the subject.