Wednesday, March 07, 2007

How do you pick research problems?

This post was inspired by a series of comments to my shameless self-promotion post. In my interview with John, I mentioned that one of the things I really like about my job is the freedom to work on whatever research problems I like. Both Iris and Anna then asked excellent follow-up questions about selecting research problems. Iris is coming at this from the leaving-the-PhD-nest angle (how do you pick research problems post-PhD?), while Anna is applying to graduate schools and wants to know how to go about picking a research problem for your Master's or PhD thesis. I thought that each of these questions was important and interesting enough to warrant a separate post, so here goes.

First, here's Iris' original question: "How do you recommend us new PhD graduates pursue being active researchers, where we tackle new ideas without spending ages in literature Review sort of thing?"

Everyone finds something different that works for them, of course, but a good place to start is with your thesis work. There's always the spin-off-as-many-papers-as-you-can approach, which definitely should be done (easy, or at least easier, pubs), but this doesn't really address the issue of "how do you start your own research program, separate from your advisor?" A good place to start is, again, with your own thesis. I found that there were questions that I didn't have time to address in my thesis. In addition, as my thesis work progressed, I found myself thinking of other, peripheral problems, things that were sort of tangential to my thesis work, but still related. Once I finished the thesis, I had time to explore these ideas a bit further.

The thing I found most useful, though, was keeping an open mind and, most importantly, talking to other researchers. I did read a lot, post-PhD. I explored some related areas that I thought I might be interested in. I talked to a lot of people to find out what they were working on. And in the midst of all this, I got the inspiration for my current line of research (and, by talking to people, found my original collaborator too, who really helped me refine my idea). I guess my research path was kind of serendipitous. But keeping an open mind and being willing to think creatively about how you want to contribute to the field can help foster new research ideas, I've found.

(Of course, I'm really curious to find out what's worked for others, too. Chime in the comments, O Seasoned Researchers, CS and non-CS alike!)

Then, Iris asks a follow-up: "do you prefer the CfP line of research (have a CfP then work on a problem to publish a paper) or do you prefer the do your own research and whenever a decent CfP appear in the horizon go for it?"

This is a great question! I tend to do the latter, almost exclusively: I work on my own research and constantly monitor the calls for papers for appropriate venues. I find that there's not enough lead time, usually, between when a CfP comes out and its deadline, to come up with a problem and a decent solution---maybe I'm a slow worker that way. :) That said, I will sometimes be inspired to finish up a particular piece of a project in response to a CfP, and get something out earlier than anticipated. (The conference paper I'm putting together now, actually, is one of those things. It's research that I wasn't sure what to do with, originally, but the CfP inspired a particular framing of the work in a way I hadn't thought of previously.) I do also have a rough idea of the deadlines of the main conferences in my field---these don't change much year to year, so I also try to structure my work so that I can meet at least a few of those deadlines.


Now, here's Anna's comment and question on the issue:

I've been looking around at master's and doctoral programmes.
Unfortunately, they seem to want me to give a description of what I'd like to research - and right now, I haven't a clue. Pretty much most things sound interesting, and it seems impossible for me to judge what areas might actually have achievable and relevant stuff to do, because I don't know anything yet.

So, how do you come up with ideas at the MSc/PhD stage? Is it common for undergrad students who go on to further study to have One Big Thing they want to look at, or is it fairly common for people to be a bit vague and undecided?


This is another great question! And while I was mulling over my answer, I found a link (thanks, John!) to a series of posts from the blog Computational Complexity on being a graduate student. There's a post on graduate school apps, where the whole "how important is the research statement?" question is addressed, but there's also a post on how to pick a research problem. There's some good advice in that post; the author's main point is that reading the current literature (conference proceedings) in whatever field interests you is a good way to figure out both what people are working on currently and what questions are out there remaining to be answered.

I think it is fairly common to only have a vague idea of what you want to do, coming out of your undergraduate years. After all, your undergrad education gives you breadth but almost no depth. If you've done some research as an undergrad already (which I highly, highly recommend to any CS undergrad even remotely considering grad school), then you've either found an area that's interesting to you or ruled out an area that you want nothing further to do with....both good things. :) Or, you've probably taken a class that really caught your interest. Either way, you now have a starting point.

One thing you can do while still an undergrad is talk to your professors: the ones you're doing research for, or the ones who are teaching the classes that are catching your interests. Go to their office hours. Let them know you're interested in the field. Ask them where to go to read up on the field further. Let them know you're thinking, maybe, of pursuing the topic in grad school. Unless they are jerks, they will be thrilled to talk to you and give you some pointers. You can also do this your first year in grad school---talk to your advisor, if you have one; otherwise, take classes that sound interesting and talk to the profs teaching those classes.

(Hmmm, I guess the advice I'm giving to Iris and Anna is not so different after all! It all boils down to "find what interests you, read a lot, and talk to a lot of people", apparently.)

Anyway, those are some of my thoughts on the whole picking a research question dilemma. Again, I would love to hear comments, both from other CS people and from the non-CS people out there---how is it different in your field, in your life, at your institution? What's worked and not worked for you?

7 comments:

A fellow junior academic said...

From a non-CS (but still slightly related) field - your advice is good. I've found that talking to people is absolutely the best way to find new research area. For me, talking to industry has been especially useful, as they often have very interesting and immediate questions that often get overlooked by academics.

I also second the advice for undergraduates to do research. In addition to giving you insights into how research "works" and finding topics that may be of interest, it's a great differentiator between you and other applicants (few undergrads do research). It also will make for a very nice letter of recommendation. Finally, talking to your professors is always a good idea - I know I love talking to students. You may learn something ;-), and your professor will be much more likely to remember you and be able to write a meaningful letter of recommendation.

Iris said...

Hi Jane,

Many thanks for giving us these lovely insights.

Regards
Iris

Jane said...

Junior Academic, I love your advice about talking to industry people, too. You can find out a lot about the state of the field from talking to them, since they are in a lot of ways closer to the action than us academics. Thanks for the tip!

PA said...

This probably doesn't matter as much for CS majors, but something I wish that I had been told when I started my PhD program was to make sure that you consider the equipment your lab has available. I spend way too many hours looking up very interesting ideas that never could have happened because we didn't have that sort of fancy equipment. Even if it is in another department, whoever owns the equipment is going to give their group priority.

Also, though you want your research to be your own, don't stray too far from the expertise of your group or you could find yourself many months behind, and without an ideal amount of support. Finally, make sure that the questions you decide on really are ones that you are interested in. This will make the drudgery of grad work much more manageable. If you don't know, start along a path, be flexible, and see where it leads.

Anonymous said...

Read, read and read some more! Don't just limit yourself to "A" journals ... sometimes papers in "B" journals leave more questions unanswered. I generated a sequence of 15 research papers out of an idea from a short note I read in SIGCSE Bulletin! You can find inspiration and problems that are *fun* for you in lots of places.

I also keep a couple deadlines: I will look at an idea for about 2 days, and if I can't find a good, precise problem to work on, I throw it away (or at least leave it in my file). Once I start working on something, know when it is the right time to give up if you can't solve it (or know when to present it to a colleague for their input). For me, I might give up after a couple weeks if I make no progress at all and a couple months if the progress is only minimal.

Jane said...

Great advice, pa and anon!

pa, being flexible *is* very important, and I'm glad you brought that up. I've found that checking out the equipment that a lab has is also important in CS---what platform is everyone using, what does the IT department think about supporting other platforms, how supportive is IT/the lab manager in getting you the machines and software that you need, how do software licenses work, etc.

anon, I'm a big fan of putting work aside or leaving it altogether if it's not working. In fact, the paper I'm working on right now involves a project I put aside for almost an entire year, and I just now figured out how it would fit into the rest of my work. So you just never know.

Anna said...

Anna here - just wanted to say thank you so much! Apologies for taking so long to return - end of semester and multiple deadlines got in the way.

Am busily reading and chewing over all the ideas here. It hadn't occurred to me to look in current papers for open questions - I'm not sure why, because I do read a fair bit - but in a very very scattered way as all my access is online, I don't think I read the same journal twice while link hopping. Hopefully this summer I can do some more directed reading.

I like the suggestion to talk to industry - and have discovered that there's actually an industry focused doctorate in the UK - the EngD. You spend 75% of your time working with an industrial sponsor on problems relevant to their business. Very interesting, as I've always found it easier to work on stuff if I know someone else is waiting for the results...

Lots of food for thought. Thank you!