Biocurious is a weblog about biology, quantified.

Doing High Impact Research

by Andre on 10 January 2006

Figuring what kind of research has impact is one thing, but figuring out how to do it is another thing entirely. When I wrote about high impact work last time, I was planning on following it up directly with a post about a talk given at Bell Labs by Richard Hamming, but I couldn’t remember his name or where I had first read the transcript of his talk. So I was very excited when I came across a link to it at Young Female Scientist’s blog the other day. You can find a transcript of the talk at Gabriel Robins’ site.

Richard Hamming was quite a successful mathematician in his own right, but the reason you should listen to his opinions on “outstanding work, the type of work that gets the Nobel Prize” is because he’s worked with and studied a whole host of incredible researchers. During his time at the Manhattan Project and at Bell Labs during the glory days, he asked himself what separated the great researchers that made a lasting impact from all the other smart people that never really lived up to their potential. What keeps good people from being great?

Luck favors the prepared mind. Hamming concedes that luck plays a role, but he still claims that there is often repetition from great researchers: they don’t just make one great contribution, they do it again and again. For an extreme example, think of Einstein. Luck might determine which particular problem is solved, but some people are clearly on track to do something great.

For example, when I met Feynman at Los Alamos, I knew he was going to get a Nobel Prize. I didn’t know what for. But I knew darn well he was going to do great work. No matter what directions came up in the future, this man would do great work. And sure enough, he did do great work. It isn’t that you only do a little great work at this circumstance and that was luck, there are many opportunities sooner or later. There are a whole pail full of opportunities, of which, if you’re in this situation, you seize one and you’re great over there instead of over here. There is an element of luck, yes and no. Luck favors a prepared mind; luck favors a prepared person.

Work on big problems and have courage. You need to have the courage to tackle big problems but you also need to take the time to identify big problems. Talk to people with big ideas, think broadly. Hamming talks about sitting at the physics table for lunch while he was at Bell Labs because that’s where the action was. When the most interesting people left (they got Nobel prizes), he found other people to eat lunch with. But beware,

`important problem’ must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn’t work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It’s not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important.

Embrace ambiguity.

Great scientists tolerate ambiguity very well. They believe the theory enough to go ahead; they doubt it enough to notice the errors and faults so they can step forward and create the new replacement theory. If you believe too much you’ll never notice the flaws; if you doubt too much you won’t get started. It requires a lovely balance.

Stay fresh Age is often considered important, especially for theoretical physicists, but Hamming believed that it’s not age itself that’s important but things that correlate with age in many cases. First, ”...if you do some good work you will find yourself on all kinds of committees and unable to do any more work” and second after a great discovery people feel pressure to do something great again so they can’t work on small problems anymore, they “fail to continue to plant the little acorns from which the mighty oak trees grow.” He also recommends switching fields every seven years. In his opinion that’s about the time it takes for you to use up a lot of your good ideas on a given topic.

You need to get into a new field to get new viewpoints, and before you use up all the old ones. You can do something about this, but it takes effort and energy. It takes courage to say, ``Yes, I will give up my great reputation.’’ For example, when error correcting codes were well launched, having these theories, I said, ``Hamming, you are going to quit reading papers in the field; you are going to ignore it completely; you are going to try and do something else other than coast on that.’’ I deliberately refused to go on in that field. I wouldn’t even read papers to try to force myself to have a chance to do something else.

Work smart He talks a lot about working hard and being emotionally committed to your work but also not wasting your time. Sounds obvious, but he has a lot of advice on how to do it. He talks about using the system instead of fighting it and being smart about who you choose to talk to. Don’t waste your time talking to people that just agree with what you say; talk to people that challenge and stimulate you and give you new ideas. Also, keep your door open. The payoff in terms of contacts and ideas outweighs the cost of interruptions in the long run.

Sell your work. Maybe undesirable (“I shouldn’t have to sell it if it’s really great work”), but given the volume of research published every hour I’m sure it’s pretty important if you want to get credit for your great work.

Those are Hamming’s main points. If you have the time, it’s worth reading the whole talk for the sake of the anecdotes alone. I found the talk pretty motivating since it gave me the impression that great work was within reach, if you’re willing to totally commit yourself to research. In Hamming’s opinion, if you want to do great work you need to pick the people you have lunch with, the problems you choose to work on, the hours you spend at work and those that you spend thinking about your work at home, all based on how it will advance your all-important research. He even admitted during his talk that he neglected his wife in favour of getting more work done.

You can lead a nice life; you can be a nice guy or you can be a great scientist. But nice guys end last, is what Leo Durocher said. If you want to lead a nice happy life with a lot of recreation and everything else, you’ll lead a nice life.

And the worst part? He’s probably right.



  1. sennoma    4148 days ago    #
    Great minds blog alike (http://www.sennoma.net/main/000016.php). Or something. I still don’t want to think Hamming’s right.
  2. Andre    4148 days ago    #
    And fools seldom differ… Needless to say, I agree with you. One aspect of the talk that really resonated with me was his observation that most people aren’t even trying to do something significant. I often get that impression when I look around. Then again, I know from my own experience that it’s not as easy as Hamming makes it sound. It’s not like I’m on track for a Nobel prize! Besides, as you mentioned in your post, one good reason not to worry about “significance” is that most people are probably working on things they find interesting and are happy with that. Perhaps Hamming overemphasizes the a goal-oriented approach to science instead of celebrating the creative process that so many of us love.
  3. PhilipJ    4148 days ago    #
    One big aspect of doing high impact research that no one seems to mention is that as a graduate student you have (in some cases) relatively little power over what you really end up doing. Projects have a way of changing as a function of time, and often in ways that aren’t controllable by the student. But you have to do reasonable research as a graduate student to even get that first post-doc and professorship, which is the first time in which I think you can really embrace a lot of the suggestions given by Hamming (and others).
  4. Andre    4148 days ago    #
    That’s a good point. The threat of a bad reference means your supervisor can veto any ideas they don’t want you to pursue (even if that idea is graduating in less than six years!). I’ve been very lucky so far that I’ve had the flexibility to work on projects I find interesting, but I realize that’s not the case for everyone.

Name
Email
http://
Message
  Textile help