My PhD advisor is proposing an unfashionable topic

Question

I am second year PhD student in pure mathematics in Europe. My PhD advisor is a well-known and respected professor who has done and still does great maths.

During the first year and a half, I have been working in a quite hot topic (say some Annals papers in the last years) which I have liked and where I have been able to produce some (not very interesting) results. My advisor produced some theorems in this topic previously, but he is not an expert on it. Recently, he recommended that we move on since he doesn't know of any further interesting and approachable problems in this area. Nonetheless, he seems to have a good (or at least not bad) opinion of me.

The problem is that the new topic he is proposing is not very fashionable. Many years ago this was a very thriving topic where he produced top results. In fact, he probably is the leading expert on this. But in the last years there have been few articles on the topic, where few is an understatement. Also, this new problem is very far from the original one. Moreover, the PhD student that worked on this has left the graduate program (which of course might only be a coincidence).

What options do I have? I am scared I won't be able to find good postdocs if I devote too much time to this. Also, he is not forcing me to work on this. But I guess that if I refuse his problem, then I should come up with some problem to study, something which I find very hard to do.

EDIT: Thanks everyone for your answers! I will meet again with my advisor and ask him further questions about the problem he is proposing: whether its feasible, why no one has tried to solve it before (maybe its too hard, requires very new techniques, almost nobody has the necessary tools, is too technical, ...), whether he thinks it is interesting for the (mathematical) community, ... But right now I think I might give it a try at least. I'll keep reading the literature on my current problem though.

Other comments:

1. I am not planning to change advisor as I am very happy with him both as a person and as a mathematician.
2. When I am talking about this hot topic in mathematics, it is not that hot. What I mean is that it has some activity and some (very) good results have appeared in the last years. Almost all these results come from a small set of authors though (which does not include my advisor).
3. By "forgotten" topic I mean a topic with few papers in ArXiv and few citations. Nonetheless, many of the techniques used to study this topic are alive and relevant in neighbouring fields.

Answer 1

I think you mistake how fashion works in mathematics.

Topics become fashionable when people produce interesting results (especially when those results are related to other areas) and become unfashionable as time passes without progress.

So, if you prove something interesting and applicable (to other mathematics, not necessarily to something outside mathematics), then you will suddenly make that area fashionable. (And interesting is more important than applicable.)

The best spot for a mathematician is to be a leader of fashion, not a follower. The most common way to become a well-known mathematician is to create a new (or revive a formerly) fashionable area that other people than follow; doing something big in an already fashionable area with lots of competition is actually much more rare (because if lots of people are working on a problem and can't solve it, chances are the problem is very hard).

Answer 2

Don’t put all your eggs in one basket!

You say in comments that “He [advisor] is saying now that he doesn't see how to continue it [your initial work in the fashionable topic]. But, to be honest, I don't know how to continue with it either.” Based on that, your advisor’s suggestion to work on other topics is probably good: you don’t want to spend too much of your time on something where you’re not very confident of progress (especially since in a fashionable field, the problems remaining open are likely to be hard).

At the same time, your concern about putting all your work into an unfashionable field is reasonable. I suspect it’s a bit overstated — if your advisor can see good problems to work on, I doubt the field can be as dead as you paint it, and (good) hiring committees will respect substantial work in an unpopular field better than weak work in the month’s hot topic. But working on this doesn’t mean abandoning everything else!

So generally I’d advise: Make sure to spend a good portion of your time on problems where you have good confidence of progress — and the less-fashionable problems your advisor is suggesting sound like the best of the options you mention here. But spend some time reading + thinking about other topics too — breadth of interests is always good, and especially with any dissatisfaction about your primary topic. And these side interests can well include continuing to think about your initial more-fashionable topic.

Answer 3

I think you should work on something that your advisor is very familiar with. How are you going to ask questions about the things you don't understand? Your advisor wouldn't be able to help you and you would have to talk with outside researchers. That's certainly something you should do, but then what would be the point of working with that advisor?

If you want to work on a particular subject, then I think your advisor should be a leading expert on that subject. I suggest looking for other potential advisors who work on the topics you are interested in.

Answer 4

I don't know how it works in math, but in physics, being unfashionable can be a career ending move. Something that you do must set you apart from your colleagues who will graduate at the same time with you and will search for jobs at the same time with you.

The pro's for being unfashionable in your case are that you can use your adviser as a resource, you have a lower chance to be scooped if you're working on something, and there is a small chance you can start something new that becomes fashionable, as others above mentioned.

But, there are many downsides. If you don't go with the herd, you will get few citations, you are less likely to be hired by fashionable professors, if you stay in academia, you get less chances to meet like minded people for future collaborations, and so on. If you get to stay in academia, you'll also be a lot less likely to get grants, because those, by tradition, mostly go to the people working on hot topics.

There are also some problems with keeping up with fashion. One is that you can never be as fashionable as the people who started the fashion. In physics, the guy who starts a subfield typically gets a few thousand citations for their seminal contribution. The rest of the people get one or two orders of magnitude less visibility.

Another issue is that every time you dive into a new field, there is a very steep learning curve. If your adviser is a specialist, you can learn things faster, if not, you need to search for collaborators and stick with them.

If you are already independent enough to do well in a more fashionable field even without your adviser, you can go for it. If it was me, I would choose a field that was fashionable, and where some my adviser's experience was relevant. That way you can get both worlds: you can stay fashionable and have a chance to combine what you know from the new field with your adviser's experience for creating something new.

I think you should voice your concerns to your adviser and try to propose something that you could do together.

Answer 5

From my dealings with professors in STEM, I'd say go with your gut and delve into your own preferred topic. If you feel strongly about a given area, you will arrive at your core idea through your own attempts. However, I know nothing about time constraints and resource issues that you may be facing or whether it is a do-or-die scenario. If you need a good postdoc, just take your time and avoid being cornered by the prof. It appears to me he just doesn't have the interest to help you set off and cover ground in your preferred area, but if you can cover enough ground privately and present some volume, he will tag along. The other alternative is to pick your area of interest and only start by discussing issues of scope with him. Let him contribute to scoping down or up while you abstract your core interest - but slowly lead him to bring up these interests. Side Note: I always looked at the postdoc as a solo project that would shape my career identity and how I view the world of biostats. So if I felt blockaded by the supervisor in any way, I would just do more private reading and ambush him with a whole new perspective that puts me back in control.

Answer 6

Recently, he recommended that we move on since he doesn't know of any further interesting and approachable problems in this area.

Do you know of any further interesting and approachable problems in this area? Or at least do you have an inkling? If you are creative / original / independent-minded (whichever term you prefer) enough to be able to come up with a (possibly quite rough) proposal on how to continue on this topic, by all means put this to your adviser. The two of you may be able to hammer out a way to continue on this. However, if the adviser does not see your ideas feasibly ending in a good thesis, you could be well-advised to follow his lead on what to do next.

On the other hand, if you have no ideas of your own on how to proceed in the "hot" area, a switch is probably for the best.

(BTW I feel that this is the sort of conundrum that student and supervisor should be able to work out between them, so it seems curious that it appears on this forum. Students sometimes think of their supervisors as semi-deities, and sometimes supervisors regard themselves as such. This does not always make for open lines of communication.)

Answer 7

You are receiving some very wise advice.

Mine is along the lines of other people's suggestions. Follow your advisor's opinion and, at the same time, read what you like to build up expertise on a different topic. Base on this additional expertise, you could be able to write a study you'd like.

You do not need a Copernican revolution. Read recent literature, say, last 10 years (very arbitrary time horizon which might vary from field to field), and put a heavier weight on the last 5 years (another arbitrary horizon).

Then, try to twist, just a little bit, some of the recent ideas for a study of yours. E.g. in economics, studies of discrimination focus on ethnicity/race and gender, while studies on discrimination based on disability or gender identity are much limited in numbers; this literature is being developed only in the last few years. These studies focus on discrimination in the labour and housing market, while there are only a few studies on discrimination based on disability or gender identity in the service market. A researcher who investigates a related topic is surely going to contribute in a meaningful and novel way, while facing limited risks.

It is hard to find a balance between ambition and risk. Much luck with it! Please get back to this post in later stages of your PhD and tell the readers how it went, it will be a useful experience for other students in your situation (I was in a similar one and I have acted accordingly to my suggestions in my answer)

Answer 8

I was in your position as a math Ph.D. student. I frankly took the route of doing my own problem (with my advisor telling me he doesn't have intuition about the problem but would be able to check my work and offer what advice he could.) This turned out great for me and I'm now tenured. But obviously there was luck involved in that I happened to stumble on just the right difficulty of a problem!

You could convey your concerns about your advisor's problem and see what he says. Ask for another problem! If he doesn't have another problem for you, and you don't want to do your own thing, then realistically you should look for another advisor. If you want a research career then I wouldn't play games with obscure topics (unless you're a genius who will raise eyebrows no matter what problem you do!) My advisor IS that caliber of a mathematician. I'm not...

Just my two cents.

Answer 9

A pragmatic perspective may involve asking yourself how badly/soon you want/need the PhD?

You earn the chance to defend a dissertation when your advisor is willing to vouch for you with their colleagues on your committee. Your defense is bolstered when the same advisor can highlight to your committee evidence of an advance/contribution: your coauthored publications and your growing reputation in the advisor's niche research community. Following your advisors research arch may offer the best chance at securing these conditions in the shortest amount of time.

If your advisor is senior, has a track record of getting people through, and your personalities are somewhat compatible, I would trust them and get it done. You can earn your first Nobel as a postdoc.

Answer 10

I think you may be getting too hung up on how you perceive your contribution to the field at the present moment, but not in the long run. Firstly, your priority is to graduate, so if you waver between old and new problems, what's fashionable or not, you may get off track -- at which point you'll eventually need your advisor to get back on track. Recall, however, that working on a PhD is supposed to entail unsupervised research, not supervised, so if you do venture on your own track, it may be harder for your advisor to get you back on track.

Most of my PhD classmates worked in fields other than my(our) advisor's, mostly because they came into the program with their own ideas. I tried going down the same path of my advisor's but eventually hit a dead end in the road years later, since things didn't pan out after I needed input from some of his colleagues. At that point, however, I had already done so much work that I only needed to parameterize some key equations in order to finish.

Because your advisor has offered to "pave the road" for you in his area of specialty, then I would think it would be rather comfortable to seek his advice whenever you get stuck. After all, no one else in the world may know the answer - including you.

One more thing - it's highly likely that what you do for your dissertation won't even be closely related to what you do once you gain employment in academia or industry. To thrive in academics or industry, you have to be a SWAK (Swiss army knife) of sorts, which implies that the narrow bandwidth of your dissertation will hardly be amenable for tackling future challenges.

What typically happens is that some time in your career you will need to draw on what you did your dissertation on, and during that moment you can refer to your seminal papers. At that point, your contemporaries and superiors will respect you more - but it usually only happens once or twice. The other angle you can take is to pursue your advisor's suggestion (track), and then publish on applying it to other areas. Then, when colleagues run across the area, they will observe that you have done most of the recent work in that space.