Monday, October 12, 2009

On the virtue of NOT working on a problem

Semester has hit with a vengeance, and while I've been busy (among other things) with this and this, my clustering series has gone on temporary hiatus, hopefully to return shortly.

In all the pages and pages of advice given to grad students, postdocs, and starting faculty, I think one item tends to get left by the wayside, or at least is not explicitly stated.
You always underestimate the time spent managing a project from start to finish.
What I mean is this: problems (at least in theoryCS) are easy to state, and fun to work on. Sometimes they take a while to crack, and sometimes they give up their secrets easily. But the time you spend on any given project is much more than the actual time spent thinking about it. There's
  • Writing up the first few drafts
  • Iterating to get a polished submission version
  • (...this step repeats until the paper is accepted)
  • Preparing the final (often very cramped) version
  • Making slides for the talk/talks you'll be giving
  • Preparing a full/journal/arxiv version, which often involves simplifying, rewriting, reproving, adding new references, etc etc.
  • Submitting to a journal, and waiting endlessly for updates on its status.
  • Addressing reviewer concerns, and resubmitting
  • And finally, getting it into print.
The few-months thrill of actually thinking about the problem and solving it ends up being a multi-year odyssey filled with many fallow periods punctuated by bursts of activity.

It's not so much the time involved - papers tend to time-multiplex quite well so you're usually in different phases of the above sequence for different papers.

It's more a matter of motivation. I don't think I'm the only person who feels this, but once I have some nice results, and especially if there isn't follow-on work to be done, I get bored with a paper. Having to deal with it for months and months afterwards is then as excruciating as killing off zombies that keep coming back (not to mention what happens if it keeps getting rejected).

So be careful when you choose a project: make sure it can last through at least a few papers, or you'll be spending a lot of time cursing yourself for the time you spend.


  1. An relevant song lyric: "Every good idea becomes a life's work for someone."

  2. I've been convinced for some time that the main difference between the great researchers and the so-so researchers is "problem picking".

    Execution is important, but you can never recover from a bad initial choice.

  3. I am a big fan of picking a direction of research as opposed to a single problem. To me, the biggest advantage of picking a direction that you can write several papers in, is that the startup time that one needs to learn about a specific problem enough to have interesting ideas for solving it, is amortized over several papers.

  4. Oded Goldreich's opinion piece "On our duties as scientists" seems relevant here:

    Particularly relevant is the quotation: "...not communicating new knowledge to the relevant scientific community is effectively equivalent to not obtaining it at all."

    --Anon. 2

  5. "[O]nce I have some nice results, and especially if there isn't follow-on work to be done, I get bored with a paper."

    I agree. Once I see that something is going to work, it gets a lot less fun. That's why I enjoy working with graduate students: they keep the momentum going. After all, they have a vested interest in seeing the paper through to publication.


Disqus for The Geomblog