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You and Your Research

  1. May 30, 2005 #1

    Gokul43201

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    What follows is a transcript of a colloquium speech given at Bell Labs, by Dr.
    Richard W. Hamming, a Professor at the Naval Postgraduate School in
    Monterey, California and a retired Bell Labs scientist.



    It's a pleasure to be here. I doubt if I can live up to the introduction. The title of my talk is, "You and Your Research.'' It is not about managing research, it is about how you individually do your research. I could give a talk on the other subject - but it's not, it's about you. I'm not talking about ordinary run-of-the-mill research; I'm talking about great research. And for the sake of describing great research I'll occasionally say Nobel-Prize type of work. It doesn't have to gain the Nobel Prize, but I mean those kinds of things which we perceive are significant things. Relativity, if you want, Shannon's information theory, any number of outstanding theories - that's the kind of thing I'm talking about.

    Now, how did I come to do this study? At Los Alamos I was brought in to run the computing machines which other people had got going, so those scientists and physicists could get back to business. I saw I was a stooge. I saw that although physically I was the same, they were different. And to put the thing bluntly, I was envious. I wanted to know why they were so different from me. I saw Feynman up close. I saw Fermi and Teller. I saw Oppenheimer. I saw Hans Bethe: he was my boss. I saw quite a few very capable people. I became very interested in the difference between those who do and those who might have done.

    When I came to Bell Labs, I came into a very productive department. Bode was the department head at the time; Shannon was there, and there were
    other people. I continued examining the questions, "Why?'' and "What is the difference?'' I continued subsequently by reading biographies, autobiographies, asking people questions such as: "How did you come to do this?'' I tried to find out what are the differences. And that's what this talk is about.

    Now, why is this talk important? I think it is important because, as far as I know, each of you has one life to live. Even if you believe in reincarnation it doesn't do you any good from one life to the next! Why shouldn't you do significant things in this one life, however you define significant? I'm not going to define it - you know what I mean. I will talk mainly about science because that is what I have studied. But so far as I know, and I've been told by others, much of what I say applies to many fields. Outstanding work is characterized very much the same way in most fields, but I will confine myself to science.

    In order to get at you individually, I must talk in the first person. I have to get you to drop modesty and say to yourself, "Yes, I would like to do first-class work.'' Our society frowns on people who set out to do really good work. You're not supposed to; luck is supposed to descend on you and you do great things by chance. Well, that's a kind of dumb thing to say. I say, why shouldn't you set out to do something significant. You don't have to tell other people, but shouldn't you say to yourself, "Yes, I would like to do something significant.''

    <contd.>
     
  2. jcsd
  3. May 30, 2005 #2

    Gokul43201

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    Let me start not logically, but psychologically. I find that the major objection is that people think great science is done by luck. It's all a matter of luck. Well, consider Einstein. Note how many different things he did that were good. Was it all luck? Wasn't it a little too repetitive? Consider Shannon. He didn't do just information theory. Several years before, he did some other good things and some which are still locked up in the security of cryptography. He did many good things.

    You see again and again, that it is more than one thing from a good person. Once in a while a person does only one thing in his whole life, and we'll talk about that later, but a lot of times there is repetition. I claim that luck will not cover everything. And I will cite Pasteur who said, "Luck favors the prepared mind.'' And I think that says it the
    way I believe it. There is indeed an element of luck, and no, there isn't. The prepared mind sooner or later finds something important and does it. So yes, it is luck. The particular thing you do is luck, but that you do something is not.

    For example, when I came to Bell Labs, I shared an office for a while with Shannon. At the same time he was doing information theory, I was doing coding theory. It is suspicious that the two of us did it at the same place and at the same time - it was in the atmosphere. And you can say, "Yes, it was luck.'' On the other hand you can say, "But why of all the people in Bell Labs then were those the two who did it?'' Yes, it is partly luck, and partly it is the prepared mind; but 'partly' is the other thing I'm going to talk about. So, although I'll come back several more times to luck, I want to dispose of this matter of luck as being the sole criterion whether you do great work or not. I claim you have some, but not total, control over it. And I will quote, finally, Newton on the matter. Newton said, "If others would think as hard as I did, then they would get similar results.''

    One of the characteristics you see, and many people have it including great scientists, is that usually when they were young they had independent thoughts and had the courage to pursue them. For example, Einstein, somewhere around 12 or 14, asked himself the question, "What would a light wave look like if I went with the velocity of light to look at it?'' Now he knew that electromagnetic theory says you cannot have a stationary local maximum. But if he moved along with the velocity of light, he would see a local maximum. He could see a contradiction at the age of 12, 14, or somewhere around there, that everything was not right and that the velocity of light had something peculiar. Is it luck that he finally created special relativity? Early on, he had laid down some of the pieces by thinking of the fragments. Now that's the necessary but not sufficient condition. All of these items I will talk about are both luck and not luck.

    How about having lots of `brains?' It sounds good. Most of you in this room probably have more than enough brains to do first-class work. But great work is something else than mere brains. Brains are measured in various ways. In mathematics, theoretical physics, astrophysics, typically brains correlates to a great extent with the ability to
    manipulate symbols. And so the typical IQ test is apt to score them fairly high. On the other hand, in other fields it is something different. For example, Bill Pfann, the fellow who did zone melting, came into my office one day. He had this idea dimly in his mind about what he wanted and he had some equations. It was pretty clear to me that
    this man didn't know much mathematics and he wasn't really articulate. His problem seemed interesting so I took it home and did a little work. I finally showed him how to run computers so he could compute his own answers. I gave him the power to compute. He went ahead, with negligible recognition from his own department, but ultimately he has collected all the prizes in the field. Once he got well started, his shyness, his awkwardness, his inarticulateness, fell away and he became much more
    productive in many other ways. Certainly he became much more articulate.

    And I can cite another person in the same way. I trust he isn't in the audience, i.e. a fellow named Clogston. I met him when I was working on a problem with John Pierce's group and I didn't think he had much. I asked my friends who had been with him at school, "Was he like that in graduate school?'' "Yes,'' they replied. Well I would have fired the fellow, but J. R. Pierce was smart and kept him on. Clogston finally did the Clogston cable. After that there was a steady stream of good ideas. One success brought him confidence and courage.

    One of the characteristics of successful scientists is having courage. Once you get your courage up and believe that you can do important problems, then you can. If you think you can't, almost surely you are not going to. Courage is one of the things that Shannon had supremely. You have only to think of his major theorem. He wants to create a method of coding, but he doesn't know what to do so he makes a random code. Then he is stuck. And then he asks the impossible question, "What would
    the average random code do?'' He then proves that the average code is arbitrarily good, and that therefore there must be at least one good code. Who but a man of infinite courage could have dared to think those thoughts? That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.

    <contd.>
     
  4. May 30, 2005 #3

    Gokul43201

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    Age is another factor which the physicists particularly worry about. They always are saying that you have got to do it when you are young or you will never do it. Einstein did things very early, and all the quantum mechanic fellows were disgustingly young when they did their best work. Most mathematicians, theoretical physicists, and astrophysicists do what we consider their best work when they are young. It is not that they don't do good work in their old age but what we value most is often what they did early. On the other hand, in music, politics and literature, often what we consider their best work was done late. I don't know how whatever field you are in fits this scale, but age has some effect.

    But let me say why age seems to have the effect it does. In the first place if you do some good work you will find yourself on all kinds of committees and unable to do any more work. You may find yourself as I saw Brattain when he got a Nobel Prize. The day the prize was announced we all assembled in Arnold Auditorium; all three winners got up and made speeches. The third one, Brattain, practically with tears in his eyes,
    said, "I know about this Nobel-Prize effect and I am not going to let it affect me; I am going to remain good old Walter Brattain.'' Well", I said to myself, "That is nice.'' But in a few weeks I saw it was affecting him. Now he could only work on great problems.

    When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn't the way things go. So that is another reason why you find that when you get early recognition it seems to sterilize you. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren't good afterwards, but they were superb before they got there and were only good afterwards.

    This brings up the subject, out of order perhaps, of working conditions. What most people think are the best working conditions, are not. Very clearly they are not because people are often most productive when working conditions are bad. One of the better times of the Cambridge Physical Laboratories was when they had practically shacks - they did some of the best physics ever.

    <contd.>
     
  5. May 31, 2005 #4

    honestrosewater

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    Thanks, that was great. I read the rest on another site- just google.

    There's one thing that worries me: sharing your work with others. Has anyone found a way to deal with this? I'm not talking about losing credit for something; I'm talking about losing the problem, the chance to work on it. That is, if there's a problem that you feel, in so many words, you were born to do, a problem that would challenge and fulfill you like none other, how do you deal with the fear that it will be solved by someone else? This would be genuine loss, at least to me. (I'm talking about a problem that requires a significant commitment and isn't really worth working on once it's solved.)
    I don't see as a solution hoping that another problem would come along. The problem being solved is great and (possibly) benefits others, and I think sharing your work is good and so on, but the fear is still difficult to deal with. Do you just have to face it and work? Is there something else to consider?
     
  6. May 31, 2005 #5
    great and interesting thread Gokul

    marlon
     
  7. May 31, 2005 #6

    Gokul43201

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  8. May 31, 2005 #7
    Very informative, tells a lot about research life and what problems an average scientist has to cope with.
     
  9. May 31, 2005 #8
    i read that from starting till end although it consumed my lot of time but i would say i gained a lot after reading that
    very informative
     
  10. May 31, 2005 #9

    ZapperZ

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    Don't you find it ironic, Gokul, that this was given at Bell labs considering that this is where the Schon debacle happened? :)

    Or maybe, it is because of the Schon debacle that the Bell Labs people need to be reminded of such thing.

    Zz.
     
  11. May 31, 2005 #10

    Gokul43201

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    Zz,

    Hamming's talk happened about 20 years ago ! I was just recently pointed in its direction, and found it to be more than just an interesting and helpful read. Besides, Hamming is an alumnus of Bell Labs.

    The Schon fraud was only a couple years ago, or so...and didn't he claim that his "non-reproducible" data resulted from error rather than deliberate manipulation ? I'm not even sure what the final verdict of the inquiry was.

    Nevertheless, I do see the irony.
     
  12. May 31, 2005 #11

    Gokul43201

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    Didn't know this existed online. Was going to cut and paste the entire thing....phew, thanks !

    This is rarely the case in the real world. Few such problems exist that someone would feel they were "born to do" with no equally worthy alternatives. Even the giant problems out there like the Millenium Problems have significant overlap. It is a disappointment to have a prize that was so close to your grasp be snatched from under your nose...but this rarely kills the spirit of a real scientist/mathmatician. Nevertheless, this fear is quite real, and pervades the scientific community at some level or the other. Some degree of secrecy is (sadly?) the norm. You will rarely come across a paper that will provide you with all the ammunition to successfully reproduce the result merely by following instructions.

    However, it is the lure of more unsolved problems, the yearning to uncover new truths or create new things; the desire to break barriers and reveal new beauty that spurs on a scientist.

    Yes, it would be a disappointment. But more often than not, the path to the solution will be different, and each path reveals new things. Besides, it would certainly not be a loss to either the scientist or the community, from a scientific point of view.

    There is no need to hope. Your wishes are already granted.
     
    Last edited: May 31, 2005
  13. May 31, 2005 #12
    Einstein was 12 or 14 and already doing stuff I still don't know about? That makes me feel retarded...

    PL
     
  14. Jun 1, 2005 #13

    honestrosewater

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    Gokul,
    Thanks, I'm getting over it. "born to do" isn't a phrase I'd normally use, but it does sum things up nicely. I'm trying to mechanize the play-writing process. Well, not the whole process (at least, not yet) but large parts of it. Okay, I shared some- baby steps. :biggrin:
     
  15. Jun 1, 2005 #14

    mathwonk

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    well just to be different, i did not enjoy that long harangue much. it reminded me of some of those phony big toothed, big jawed people on tv infomercials named maybe tony who tell you how to be empowered by adopting their system. I recommend reading something by a real intellectual commenting on how research has been done by brilliant people, such as the book by jacques hadamard, On the psychology of invention in the mathematical field.
     
  16. Jun 1, 2005 #15

    ZapperZ

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    Ooooh.. I should have looked at the date.

    Still, I find plenty of irony in there. Obviously, that talk didn't have any impact on some people there.

    The Schon's debacle is a done deal. The Beasley commission appointed by Bell Lab has concluded that he manipulated and falsified data on several papers. Bell labs and Batlogg (the lead PI on each papers) have retracted all of his papers, even those not being part of the commision's investigation.

    Zz.
     
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