
Ask HN: PhD students - how do you find a remarkable research topic? - eob
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.<p>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.<p>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.<p>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?
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yannis
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?_

~~~
eob
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.

~~~
yannis
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.

------
mechanical_fish
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.

\---

[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.

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

