How do I know what the important problems to work on are?

Question

Basically, I think research groups form "inner circles" where people generate important problems. But I am not in any of these "inner circles," so I don't know where the potentially important problems that will lead to papers in top, prestigious journals are. The people who publish in top journals know what the important problems are. However, I do not and I will never publish papers in top journals at this rate. How do I access this information without asking someone what the important questions are?

One way I can think of is to go to seminars. But I also want to know how to make an advance in the difficult problems and for that I need to discuss with the leading experts in the problem.

Answer 1

I wrote this as part of an answer on another question:

One of the things many mathematicians have trouble developing is what might be called "good taste" - a sense of what mathematics is genuinely interesting and can lead to further interesting developments. Some have so little taste that they declare that there is no such thing, and then claim the popularity of various research areas is driven purely by the entirely arbitrary decisions of famous mathematicians.

Don't fall into this trap. Problems are interesting or not for genuine mathematical reasons.

You should think that there are a small number of 'obviously interesting' problems - to pick a few that most algebraically inclined pure mathematicians have heard of - calculating the homotopy groups of spheres, understanding the moduli space of complex algebraic curves (with marked points), the Riemann Hypothesis, the Continuum Hypothesis (although in some sense this is solved), irrationality of zeta(5). Most fields of mathematics also have less famous problems that are important in part because they have been worked on but remain unsolved for a long time. Of course it's probably a bad idea to work directly on these problems.

However, because these problems are so important, any work that provides a potentially useful approach to these problems is important. That's where taste comes in. Great mathematicians have the ability to spot approaches to problems that are potentially useful, and these approaches require solving more problems, and these are the practical important problems whose solutions get published in top journals.

Anyone with the vision to find such approaches can get published in top journals. It is true that mathematicians who are close to great mathematicians can sometimes benefit by having the great mathematician point out an approach and direct them to the problems that need to be solved, but, actually, the great mathematicians generally reserve most of these problems for themselves, because it's important and they don't trust someone else to do the work.

So - the answer is - develop good taste for yourself rather than trying to rely on the good taste of others - or, like 95% or more of mathematicians, give up on being great.

Answer 2

It is difficult for anyone working strictly alone to come up with good ideas and just as hard, perhaps, to turn them into interesting results. Even Einstein worked with a circle of collaborators in the development of Special Relativity.

My advice would be to talk to a lot of people and form a circle of collaborators. Find ways to meet with them, at conferences, say, or by inviting them to your institution for talks. This is easier now with the internet than it was in the past, but it has always been a tool for researchers. It is one of the main reasons that universities were formed, of course.

Share ideas and work toward a productive group, probably sharing authorship of things that develop.

Talk to people outside your field, also: "What sort of problems do you see that need a solution?" After supper sherry hour at the Cambridge colleges are especially good at this, since the members are interdisciplinary.

You can read a lot of stuff for ideas, of course, but a group can read a lot more than an individual can. Some ideas are just serendipity, but a group can make serendipity work for you if you spend some time "thinking out loud".

Answer 3

Attend seminars, post on online forums, work more with students - it is not like these "inner circles" are some secret cabal designed to hide the information from underprivileged, they are just more intensive and, ergo, efficient, than an average seminar or a random hallway talk could be. It is people that make research groups "top", not the other way around - although is your situation is particularly bad, you could be very noticeably less productive than you could have been otherwise. Researchers flock to prestigious universities to find interesting people and ideas there; clicking with them would be a whole lot more productive than joining a leading research group where you will be a fifth wheel. Setting your sights on a handful of people and trying to squeeze into their group which already works well is setting your scope too narrow (not to mention piggybacking on others' success is a dubious tactic).

There are a few other things that I would also like to point out. First and foremost, every measure which becomes a target becomes a bad measure: publishing in top journals is a terrible goal. Because of that, "I will never publish papers in top journals at this rate" is dangerous as a shortcut for "I am concerned I will never do great research".

Next, as Hamming has elucidated (this is an amazing read overall!):

It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important.

Great scientists made breakthroughs in known problems, but those who are the first to convince others something is worth studying truly cement their place in history. Please refer to this important observation also (IMHO, this applies to all sciences, not just mathematics). "How do I make progress" is a million-dollar question, sometimes literally. There is no general advice on how to know if something is important and could lead to interesting results - as in, which ideas are worth pursuing. The answer is 42, essentially. Short of going through more ideas and training your own heuristics and intuition, there is not much to be said on this topic.

Then come the strategies. Sometimes, it is obvious that the field is "hot" and is making rapid progress, but in small steps: if you are not a member of a strong research group or do not have a good attack on the problem otherwise, it is indeed more likely that you end up producing something valuable, but not all that significant. It does not mean one should always give up or never even try, but if public recognition for some reason or another is important for you, it has to be a consideration. As stated above, maybe you could make more substantial progress by joining a group you get along with well rather than chasing the hottest trends in your area. This has its own drawbacks, of course, and there are looming risks of irrelevance.