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Ask HN: PhD students - how do you find a remarkable research topic?

6 pointseob5 comments

I stumbled upon Seth Godin's TED talk yesterday in which he presented his Purple Cow meme about the importance of being remarkable. As I listened, I couldn't help but think how true his words were, even for research.

I'm a PhD student in my second year currently searching for that topic that I'll pursue for the next few years to ultimately get a degree. One thing I've noticed looking at older students is that they fall into three camps. The first group pursues a random assortment of small projects for ~5 years and graduates with a "stapler thesis" -- essentially a grab bag thesis describing their small forays. The second group picks an obscure and incremental topic and pursues it, becoming an expert on a novel, but ultimately unexciting, phenomena.

The final group are the ones that truly succeed, and I expect are the ones that land jobs at top-tier research schools. They are the ones that manage to innovate not at the research level, but at the conceptual one. Rather than thinking up new ways to better old problems, they find a way to look at things that completely surprises/delights people when they hear about it.

So to all those PhD students out there that fall into this third category: how do you do your brainstorming? How do you identify the large-scale research themes waiting to be discovered? Is it dumb luck, inherited gift, or the result of a process that can be learned?

With hindsight I would suggest the following:

(01) Most PhD Research is unremarkable. Do some research in your field, list all PhD theses over the last 30 years and give them a score. How many made a mark on the field? My guess possibly 1/1000. You can do the same with journal papers, possibly 1/3000.

(02) Citations is not a measure of success of a research paper/topic. Is this research applied today? Is it useful?

(03) The Dons in the UK had one measure of success of a PhD. It had to advance the field and be original. Most Science advances this way. There is one major breakthrough and hundreds of small steps to advance it forward. (this would probably fall within your second group).

(04) Do a social graph on 3-5 topics. Who is working where? If you want to land in say one of the big Research Institutions, make sure that there is on-going research in this area by that Institution.

(05) Decide who you want to get married to. Your thesis supervisor would be the most important person for you over the next few years. Is he interested in the research you are interested in?

My late professor used to advise that your PhD is you license to carry out research and not your major work.

If I had to do it all over again, I would do the social graph and go from there. I would also try and get into an area that scales rather than purple cows or black swans. At the moment anything with a prefix bio is still virgin territory as far as I am concerned.

Perhaps if you could let us know your field, people might be able to give you some ideas. You could also try reposting the query as If you had three-five years to do research in Computing/field, what would you choose as a topic and why?

Thanks yannis, these are some great comments.

With regard to the social graph one, I've heard advice akin to this from several people: that the person is more important than the topic when it comes to advisors. When you look at the PhD as a license to carry out research, rather than a major work itself, this makes sense. But it is sure hard to force yourself to adopt that attitude when you're in the middle of it. From the student perspective, it is tempting to make the argument, "This professor doesn't fit my personality, but I really want to work on this particular topic."

Regarding scalability, what you say makes sense. Indeed, I am a bit jealous of people with a bio- prefix; they are in the same spot computer scientists were in a few decades ago.

As far as my personal background, I am a Computer Science guy with a background in the systems community (semantic web, databases, web architecture) who is interested in getting more into machine learning. I'd love any advice on where you think the exciting momentum is in that area.

EDIT: Re-worded for clarity.

I think there is both large scope to do research as well as exciting momentum in Large-Scale Machine Learning. As data in many domains arrives faster than we are able to learn from it, we need to switch from the traditional "one-shot" machine learning approach to systems that are able to mine continuous, high-volume, open-ended data streams as they arrive. Establishing the theoretical basis of such an approach, is still virgin territory.

You could do worse than to listen to Hamming:

http://www.paulgraham.com/hamming.html

But, having said that, when you ask:

Is it dumb luck, inherited gift, or the result of a process that can be learned?

The answer is "all of the above". You need to follow good procedures that you will learn with experience, you need to have certain qualities, not the least of which are social skills -- bad research well described will trump brilliant but poorly-presented research every time -- but do not underestimate the role of dumb luck. For every awesome research problem that turns out to be tractable, there are many that just don't pan out.

There's a story I heard about Feynman. They say that Feynman used to take on grad students, and they would ask him what to work on. Feynman dreaded these questions. If he told a student to work on Interesting Problem X, and (s)he labored on it for years, only to find that it was intractable and therefore ultimately uninteresting after all, he was afraid the student would be terribly depressed, as depressed as only a late-term Ph.D. student can be. The story was that Feynman would tell the students to come back in a day or two, then take a problem and frantically work it out as fast and as far as he could in a day, trying to get a few years ahead of the student in a few hours, far enough ahead that he could be confident that an answer was likely to exist. Then he'd hide all his notes and present the problem to the student as an interesting and novel new idea.

Unfortunately, if you aren't a theorist, and your adviser isn't quite as smart, conscientious, and downright devious as Richard Feynman was, you'll be a normal grad student: You'll work away on a problem, and maybe it will be exciting, and maybe it will be boring, and the odds are on boring. [1] The secret is not to worry about this. If you want a successful research career, just keep moving from problem to problem: Finish your thesis (yes, with a stapler if you have to -- when you gotta finish, you gotta finish) and then devote your postdocs to finding a better problem, using all those Hamming-inspired skills you've been working on.

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[1] One truism: By the time you finish your thesis you are likely to be so bored with your own project that you will want to scream. Even if your project, properly presented, is actually pretty exciting to the independent observer. You lose perspective in your fifth or sixth year. That's why it's more important to keep moving than to hold out for the perfect project, or the golden dissertation.

That is a great story about Feynman, and thanks for the Hamming article link.

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