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Monday, August 07, 2006

Optimism and Patience

When looking for a long-term partner, you may have had a long string of failed dates, but you must remain optimistic that the next one will be "the one." You must also have patience to let a relationship develop before giving up and moving on.

The same advice holds for proving theorems. When trying to prove a difficult result, particularly a well-studied open question, it often seems some evil deity finds ways to foil your many proof attempts just as they almost seem to work. Don't give up. Remain optimistic that you can prove this theorem and keep the patience trying new approaches even as each approach gets cruelly shot down. Only when you've exhausted all of your ideas should you move on to the next result.

Over the years I have kept my optimism about proving a result, but I haven't had as much patience as earlier in my research career. Partly because as one gets older one gets more non-research responsibilities both at the university and in the community, though this is more an excuse than a reason. I also find it more difficult these days to focus on a single problem for hours or days at a time.

Let this be a lesson to young researchers. Don't worry that the older famous researchers have not solved the big open questions; most (but not all) do not have as much patience to focus on a problem and explore as many of the possible proof techniques as well as you can.

22 comments:

  1. We already know how to prove theorems Lance. What we need is advice on how to get dates!

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  2. Aisle 10 (bulk foods).

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  3. Lance, this is the last advice I'd give a grad student. Almost every grad student I meet suffers from too much patience, not too little. If left to her own devices, she'll "work" on the same problem for two years without making any progress, because (having been trained on quizzes and problem sets) she's never learned how to admit failure and move on. Here's my advice: be as promiscuous as you can! Only work on a problem if you think you more or less already know how to solve it. Of course, you'll often (usually) be wrong. But here's the flip side: if you think you have no idea how to solve the problem, you'll almost certainly be right.

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  4. Scott, this is ridiculously bad advice. Every researcher has to find the right balance between perserverance and promiscuity. Indeed, this is part of the point of graduate school. And it's a very personal tradeoff- don't encourage everyone to be a slut. It feels good for the moment, but you can end up feeling cheap and dirty at the end of the day.

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  5. Well, I guess it depends on what your goals are. If you're happy increasing your paper count through incremental results, promiscuity is the way to go.

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  6. Every aspiring researcher needs plenty of practice solving problems and writing up their proofs. For me, the most fun way to achieve this is to find a good open-ended question (together with a collaborator with a compatible personality), where part of the solution is figuring out what formulation of the problem you can solve.

    On the other hand, I think that too many young researchers today are TOO focused on producing text. If you've got the energy and interest, devour as much literature as you can at this stage. If you direct your reading towards even just understanding the details of some big unsolved problem, you just might actually end up solving it, although you shouldn't expect to. That's what your postdoc is for. ;)

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  7. I think the "don't-start-till-you've-already-solved-it" approach is more likely to produce breakthroughs, not less. There are several reasons: first, every time you solve a problem (as opposed to spinning your wheels for two years and then giving up), you build up the confidence to attack harder problems. Second, the more problems you try, the more likely you are to score a hit. And third, when you do attack a big problem, it will be because you have a "special angle" on it -- you'll feel (as Feynman once put it) that you're the most qualified person in the world to attack this particular problem. Even if your "special angle" is completely illusory (as it usually will be), and even if your eventual solution has nothing whatsoever to do with it, I would never be able to get started without such an angle.

    Look at it this way: not even Wiles spent time on Fermat's Last Theorem until he felt he had a viable approach.

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  8. In response to Scott,
    (1) If you work on a hard problem for a long time, you will likely end up with some results, though not perhaps the result you want. Being excessively ambitious might be required to get anything at all...
    (2) That's just false in general, some problems do require a sustained attack. Thinking about them in a casual way is worse than useless.
    (3) For all this talk of a special angle, the fundamental requisites are interest and motivation . It's a matter of personal taste, not of having a "secret weapon".

    Finally, it's down to the researcher's personality. Someone like Ran Raz is an outstanding example of an approach diametrically opposite to yours. On the other hand, there are cases of successful researchers who like to keep several problems "on the boil". Neither patience nor impatience are easily taught, you've got to assess your strengths realistically and play to them.

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  9. I think both breadth and depth are necessary. See e.g. Seymour, he won three Fulkerson awards, however he has more than 170 published papers. Another example is Noga Alon. Even Ran Raz has more than 70 papers. So both paper count and paper depth are necessary.

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  10. Ran Raz has (by his own count on his home page), about 50 papers. Paper counts are largely irrelevant, but stop counting #DBLP entries. It's stupid. You're triple counting many papers (conf + ECCC + journal).

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  11. My personal take is to agree with Scott: start out promiscuously. Especially for beginning graduate students, I think it's important to start out by just solving something in a reasonable time frame, if only to get the hang of research, and gain some insight into what types of problems you enjoy. It is important, however, to not then forget the goal of building up to deeper, more challenging work. This worked for me (though some would surely argue I did indeed forget that last goal).

    I would recognize, however, that not everyone works best in this fashion. In graduate school, Eric Vigoda amazed me by settling on the problem of approximate counting of independent sets, and he would not let go of it, eventually obtaining his first amazing result (Approximately Counting Up to Four). His working style clearly worked for him, then and since!

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  12. Partly because as one gets older one gets more non-research responsibilities both at the university and in the community, though this is more an excuse than a reason.

    You mean, like posting to a weblog? ;-)

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  13. You're triple counting many papers (conf + ECCC + journal).

    Spealing of which, I'm always thorn in this issue. Double counting conference+journal papers is not right, but neither is single counting both papers as if there were one. If they were one and the same we computer scienties would all make our conference papers into journal versions promptly. The fact that we don't reflects that there is non-negiligible amounts of work in the conversion.

    Over the years in my CV I've gone back and forth from single counting to double counting but I'm always unsatisfied.

    Any suggestions out there about how to list journal/conference papers in a way that does justice to them, neither underselling nor overselling?

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  14. To the previous Anonymous:

    I think an easy way is to mention the journal versions and for each journal version which has a corresponding conferenc version, mention also the conference in which it appeared. Then everything should be fine. I really do not like mentioning them as two separate papers.

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  15. Any suggestions out there about how to list journal/conference papers in a way that does justice to them, neither underselling nor overselling?

    The reason to list a conference publication along with the correpsonding journal reference is as a stamp of value (since conferences are very prestigious in TCS). So there's nothing wrong with simply writing "Extended abstract..." or "Prelim. version in FOCS'87" No need to list page numbers, years, conference location, etc. and you can have a key somewhere FOCS = ..., STOC = ...

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  16. I really do not like mentioning them as two separate papers.

    I wonder if your adverse reaction comes from a misguided sense of fairness.

    You see, one solution results in undercounting, the other in overcounting, so from a purely fairness perspective both are equally undesirable.

    Moreover, if we chose simply not to give any extra count for journal versions then most people will simply choose not to spend the extra time writing the journal version, which is what happens in practice. On the other hand if we choose to overcount, then everyone (except slackers) would benefit equally from the double counting resulting in no net gain, but everyone would have the incentive to submit a complete version to a journal.

    So all in all, from a purely game theoretical perspective the strategy that maximizes the social good is to agree to double count.

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  17. So there's nothing wrong with simply writing "Extended abstract..." or "Prelim. version in FOCS'87" No need to list page numbers, years, conference location, etc. and you can have a key somewhere FOCS = ..., STOC = ...


    Then again this leads to some people publishing essentially the same paper in conference/journal versions using different titles so as to list them separately.

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  18. I really do not like mentioning them as two separate papers.

    I wonder if your adverse reaction comes from a misguided sense of fairness.

    You see, one solution results in undercounting, the other in overcounting, so from a purely fairness perspective both are equally undesirable.

    Moreover, if we chose simply not to give any extra count for journal versions then most people will simply choose not to spend the extra time writing the journal version, which is what happens in practice. On the other hand if we choose to overcount, then everyone (except slackers) would benefit equally from the double counting resulting in no net gain, but everyone would have the incentive to submit a complete version to a journal.

    So all in all, from a purely game theoretical perspective the strategy that maximizes the social good is to agree to double count.gy that maximizes the social good is to agree to double count.

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  19. This whole discussion is rather silly. The overwhelming majority of the time, a journal paper has already appeared somewhere else in preliminary form. (The only exceptions I can think of are very short journal papers, which are easy to pick out.) So listing journal pubs followed by conference pubs allows someone else to count the total number of different publications (by counting conf. pubs) as well as to couunt the number of correct publications (by counting journal pubs).

    PS: I'm kidding about the "correct", of course. But in academia, number of journal pubs is apparently important independent of number of overall pubs.

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  20. This whole discussion is rather silly.

    Actually considering how much weight is given by paper pushers to publication counts and how strongly some people feel against paper counting, it follows that either choice can have a noticeable impact on your career.

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  21. Should we consider comments 16 and 18 as a single comment or should we double count them?

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  22. I'd like to get back to commenting on the original advice from Lance's e-mail. For the most part I want to agree with Mike Mitzenmacher and Scott (to a lesser extent) rather than Lance, though Lance does have some good points to make.

    First research success is incredibly important for confidence and the understanding of what research is all about. Working fruitlessly on a single problem for a long period of time is not a good strategy for gaining that understanding. It is amazing the number of people whose research careers blossom as postdocs when they are freed from working on the one big problem from their dissertation.

    In an ideal situation you should have multiple problems on which you have a high enough level of concentration to do serious thinking. When progress on one is stalled you can shift to another and then back again. At the same time, reading broadly is also important. You may find great low hanging fruit (or ideas that are obvious to you but not others) while you are reading!

    I think that the issue Lance describes is correct in some respects. As other demands intervene, it becomes much more difficult to get into new problems sufficiently that you can really concentrate on them. Reading broadly is also harder to do because of time contraints. So, enjoy the time to explore while you have it!

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