Richard Hamming: You and Your research

Talk at Bellcore, 7 March 1986
Thetitle of my talk is, ``You and Your Research.‘‘ It is not aboutmanaging research, it is about how you individually do your research. Icould 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 talkingabout great research. And for the sake of describing great researchI‘ll occasionally say Nobel-Prize type of work. It doesn‘t have to gainthe Nobel Prize, but I mean those kinds of things which we perceive aresignificant things. Relativity, if you want, Shannon‘s informationtheory, any number of outstanding theories-- that‘s the kind of thingI‘m talking about.
Now, how did I come to do this study? At LosAlamos I was brought in to run the computing machines which otherpeople had got going, so those scientists and physicists could get backto business. I saw I was a stooge. I saw that although physically I wasthe same, they were different. And to put the thing bluntly, I wasenvious. I wanted to know why they were so different from me. I sawFeynman up close. I saw Fermi and Teller. I saw Oppenheimer. I saw HansBethe: he was my boss. I saw quite a few very capable people. I becamevery interested in the difference between those who do and those whomight have done.
When I came to Bell Labs, I came into a veryproductive department. Bode was the department head at the time;Shannon was there, and there were other people. I continued examiningthe questions, ``Why?‘‘ and ``What is the difference?‘‘ I continuedsubsequently by reading biographies, autobiographies, asking peoplequestions such as: ``How did you come to do this?‘‘ I tried to find outwhat 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 asI know, each of you has one life to live. Even if you believe inreincarnation it doesn‘t do you any good from one life to the next! Whyshouldn‘t you do significant things in this one life, however youdefine 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 sayapplies to many fields. Outstanding work is characterized very much thesame way in most fields, but I will confine myself to science.
Inorder to get at you individually, I must talk in the first person. Ihave to get you to drop modesty and say to yourself, ``Yes, I wouldlike to do first-class work.‘‘ Our society frowns on people who set outto do really good work. You‘re not supposed to; luck is supposed todescend on you and you do great things by chance. Well, that‘s a kindof dumb thing to say. I say, why shouldn‘t you set out to do somethingsignificant. You don‘t have to tell other people, but shouldn‘t you sayto yourself, ``Yes, I would like to do something significant.‘‘
Inorder to get to the second stage, I have to drop modesty and talk inthe first person about what I‘ve seen, what I‘ve done, and what I‘veheard. I‘m going to talk about people, some of whom you know, and Itrust that when we leave, you won‘t quote me as saying some of thethings I said.
Let me start not logically, but psychologically.I find that the major objection is that people think great science isdone by luck. It‘s all a matter of luck. Well, consider Einstein. Notehow 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 justinformation theory. Several years before, he did some other good thingsand some which are still locked up in the security of cryptography. Hedid many good things.
You see again and again, that it is morethan one thing from a good person. Once in a while a person does onlyone thing in his whole life, and we‘ll talk about that later, but a lotof times there is repetition. I claim that luck will not covereverything. And I will cite Pasteur who said, ``Luck favors theprepared mind.‘‘ And I think that says it the way I believe it. Thereis indeed an element of luck, and no, there isn‘t. The prepared mindsooner or later finds something important and does it. So yes, it isluck. The particular thing you do is luck, but that you do something isnot.
For example, when I came to Bell Labs, I shared an officefor a while with Shannon. At the same time he was doing informationtheory, I was doing coding theory. It is suspicious that the two of usdid it at the same place and at the same time - it was in theatmosphere. And you can say, ``Yes, it was luck.‘‘ On the other handyou can say, ``But why of all the people in Bell Labs then were thosethe two who did it?‘‘ Yes, it is partly luck, and partly it is theprepared 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 todispose of this matter of luck as being the sole criterion whether youdo great work or not. I claim you have some, but not total, controlover 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 similarresults.‘‘
One of the characteristics you see, and many peoplehave it including great scientists, is that usually when they wereyoung they had independent thoughts and had the courage to pursue them.For example, Einstein, somewhere around 12 or 14, asked himself thequestion, ``What would a light wave look like if I went with thevelocity of light to look at it?‘‘ Now he knew that electromagnetictheory says you cannot have a stationary local maximum. But if he movedalong with the velocity of light, he would see a local maximum. Hecould see a contradiction at the age of 12, 14, or somewhere aroundthere, that everything was not right and that the velocity of light hadsomething peculiar. Is it luck that he finally created specialrelativity? Early on, he had laid down some of the pieces by thinkingof the fragments. Now that‘s the necessary but not sufficientcondition. All of these items I will talk about are both luck and notluck.
How about having lots of `brains?‘ It sounds good. Most ofyou in this room probably have more than enough brains to dofirst-class work. But great work is something else than mere brains.Brains are measured in various ways. In mathematics, theoreticalphysics, astrophysics, typically brains correlates to a great extentwith the ability to manipulate symbols. And so the typical IQ test isapt to score them fairly high. On the other hand, in other fields it issomething different. For example, Bill Pfann, the fellow who did zonemelting, came into my office one day. He had this idea dimly in hismind about what he wanted and he had some equations. It was prettyclear to me that this man didn‘t know much mathematics and he wasn‘treally articulate. His problem seemed interesting so I took it home anddid a little work. I finally showed him how to run computers so hecould compute his own answers. I gave him the power to compute. He wentahead, with negligible recognition from his own department, butultimately he has collected all the prizes in the field. Once he gotwell started, his shyness, his awkwardness, his inarticulateness, fellaway and he became much more productive in many other ways. Certainlyhe became much more articulate.
And I can cite another person inthe same way. I trust he isn‘t in the audience, i.e. a fellow namedClogston. I met him when I was working on a problem with John Pierce‘sgroup and I didn‘t think he had much. I asked my friends who had beenwith him at school, ``Was he like that in graduate school?‘‘ ``Yes,‘‘they replied. Well I would have fired the fellow, but J. R. Pierce wassmart and kept him on. Clogston finally did the Clogston cable. Afterthat there was a steady stream of good ideas. One success brought himconfidence and courage.
One of the characteristics of successfulscientists is having courage. Once you get your courage up and believethat you can do important problems, then you can. If you think youcan‘t, almost surely you are not going to. Courage is one of the thingsthat Shannon had supremely. You have only to think of his majortheorem. He wants to create a method of coding, but he doesn‘t knowwhat to do so he makes a random code. Then he is stuck. And then heasks the impossible question, ``What would the average random codedo?‘‘ He then proves that the average code is arbitrarily good, andthat therefore there must be at least one good code. Who but a man ofinfinite courage could have dared to think those thoughts? That is thecharacteristic of great scientists; they have courage. They will goforward under incredible circumstances; they think and continue tothink.
Age is another factor which the physicists particularlyworry about. They always are saying that you have got to do it when youare young or you will never do it. Einstein did things very early, andall the quantum mechanic fellows were disgustingly young when they didtheir best work. Most mathematicians, theoretical physicists, andastrophysicists do what we consider their best work when they areyoung. It is not that they don‘t do good work in their old age but whatwe value most is often what they did early. On the other hand, inmusic, politics and literature, often what we consider their best workwas done late. I don‘t know how whatever field you are in fits thisscale, but age has some effect.
But let me say why age seems tohave the effect it does. In the first place if you do some good workyou will find yourself on all kinds of committees and unable to do anymore work. You may find yourself as I saw Brattain when he got a NobelPrize. The day the prize was announced we all assembled in ArnoldAuditorium; all three winners got up and made speeches. The third one,Brattain, practically with tears in his eyes, said, ``I know about thisNobel-Prize effect and I am not going to let it affect me; I am goingto remain good old Walter Brattain.‘‘ Well I said to myself, ``That isnice.‘‘ But in a few weeks I saw it was affecting him. Now he couldonly work on great problems.
When you are famous it is hard towork on small problems. This is what did Shannon in. After informationtheory, what do you do for an encore? The great scientists often makethis error. They fail to continue to plant the little acorns from whichthe mighty oak trees grow. They try to get the big thing right off. Andthat isn‘t the way things go. So that is another reason why you findthat when you get early recognition it seems to sterilize you. In factI will give you my favorite quotation of many years. The Institute forAdvanced Study in Princeton, in my opinion, has ruined more goodscientists than any institution has created, judged by what they didbefore they came and judged by what they did after. Not that theyweren‘t good afterwards, but they were superb before they got there andwere only good afterwards.
This brings up the subject, out oforder perhaps, of working conditions. What most people think are thebest working conditions, are not. Very clearly they are not becausepeople are often most productive when working conditions are bad. Oneof the better times of the Cambridge Physical Laboratories was whenthey had practically shacks - they did some of the best physics ever.
Igive you a story from my own private life. Early on it became evidentto me that Bell Laboratories was not going to give me the conventionalacre of programming people to program computing machines in absolutebinary. It was clear they weren‘t going to. But that was the wayeverybody did it. I could go to the West Coast and get a job with theairplane companies without any trouble, but the exciting people were atBell Labs and the fellows out there in the airplane companies were not.I thought for a long while about, ``Did I want to go or not?‘‘ and Iwondered how I could get the best of two possible worlds. I finallysaid to myself, ``Hamming, you think the machines can do practicallyeverything. Why can‘t you make them write programs?‘‘ What appeared atfirst to me as a defect forced me into automatic programming veryearly. What appears to be a fault, often, by a change of viewpoint,turns out to be one of the greatest assets you can have. But you arenot likely to think that when you first look the thing and say, ``Gee,I‘m never going to get enough programmers, so how can I ever do anygreat programming?‘‘
And there are many other stories of thesame kind; Grace Hopper has similar ones. I think that if you lookcarefully you will see that often the great scientists, by turning theproblem around a bit, changed a defect to an asset. For example, manyscientists when they found they couldn‘t do a problem finally began tostudy why not. They then turned it around the other way and said, ``Butof course, this is what it is‘‘ and got an important result. So idealworking conditions are very strange. The ones you want aren‘t alwaysthe best ones for you.
Now for the matter of drive. You observethat most great scientists have tremendous drive. I worked for tenyears with John Tukey at Bell Labs. He had tremendous drive. One dayabout three or four years after I joined, I discovered that John Tukeywas slightly younger than I was. John was a genius and I clearly wasnot. Well I went storming into Bode‘s office and said, ``How cananybody my age know as much as John Tukey does?‘‘ He leaned back in hischair, put his hands behind his head, grinned slightly, and said, ``Youwould be surprised Hamming, how much you would know if you worked ashard as he did that many years.‘‘ I simply slunk out of the office!
WhatBode was saying was this: ``Knowledge and productivity are likecompound interest.‘‘ Given two people of approximately the same abilityand one person who works ten percent more than the other, the latterwill more than twice outproduce the former. The more you know, the moreyou learn; the more you learn, the more you can do; the more you cando, the more the opportunity - it is very much like compound interest.I don‘t want to give you a rate, but it is a very high rate. Given twopeople with exactly the same ability, the one person who manages day inand day out to get in one more hour of thinking will be tremendouslymore productive over a lifetime. I took Bode‘s remark to heart; I spenta good deal more of my time for some years trying to work a bit harderand I found, in fact, I could get more work done. I don‘t like to sayit in front of my wife, but I did sort of neglect her sometimes; Ineeded to study. You have to neglect things if you intend to get whatyou want done. There‘s no question about this.
On this matter ofdrive Edison says, ``Genius is 99% perspiration and 1% inspiration.‘‘He may have been exaggerating, but the idea is that solid work,steadily applied, gets you surprisingly far. The steady application ofeffort with a little bit more work, intelligently applied is what doesit. That‘s the trouble; drive, misapplied, doesn‘t get you anywhere.I‘ve often wondered why so many of my good friends at Bell Labs whoworked as hard or harder than I did, didn‘t have so much to show forit. The misapplication of effort is a very serious matter. Just hardwork is not enough - it must be applied sensibly.
There‘sanother trait on the side which I want to talk about; that trait isambiguity. It took me a while to discover its importance. Most peoplelike to believe something is or is not true. Great scientists tolerateambiguity very well. They believe the theory enough to go ahead; theydoubt it enough to notice the errors and faults so they can stepforward and create the new replacement theory. If you believe too muchyou‘ll never notice the flaws; if you doubt too much you won‘t getstarted. It requires a lovely balance. But most great scientists arewell aware of why their theories are true and they are also well awareof some slight misfits which don‘t quite fit and they don‘t forget it.Darwin writes in his autobiography that he found it necessary to writedown every piece of evidence which appeared to contradict his beliefsbecause otherwise they would disappear from his mind. When you findapparent flaws you‘ve got to be sensitive and keep track of thosethings, and keep an eye out for how they can be explained or how thetheory can be changed to fit them. Those are often the greatcontributions. Great contributions are rarely done by adding anotherdecimal place. It comes down to an emotional commitment. Most greatscientists are completely committed to their problem. Those who don‘tbecome committed seldom produce outstanding, first-class work.
Nowagain, emotional commitment is not enough. It is a necessary conditionapparently. And I think I can tell you the reason why. Everybody whohas studied creativity is driven finally to saying, ``creativity comesout of your subconscious.‘‘ Somehow, suddenly, there it is. It justappears. Well, we know very little about the subconscious; but onething you are pretty well aware of is that your dreams also come out ofyour subconscious. And you‘re aware your dreams are, to a fair extent,a reworking of the experiences of the day. If you are deeply immersedand committed to a topic, day after day after day, your subconscioushas nothing to do but work on your problem. And so you wake up onemorning, or on some afternoon, and there‘s the answer. For those whodon‘t get committed to their current problem, the subconscious goofsoff on other things and doesn‘t produce the big result. So the way tomanage yourself is that when you have a real important problem youdon‘t let anything else get the center of your attention - you keepyour thoughts on the problem. Keep your subconscious starved so it hasto work on your problem, so you can sleep peacefully and get the answerin the morning, free.
Now Alan Chynoweth mentioned that I usedto eat at the physics table. I had been eating with the mathematiciansand I found out that I already knew a fair amount of mathematics; infact, I wasn‘t learning much. The physics table was, as he said, anexciting place, but I think he exaggerated on how much I contributed.It was very interesting to listen to Shockley, Brattain, Bardeen, J. B.Johnson, Ken McKay and other people, and I was learning a lot. Butunfortunately a Nobel Prize came, and a promotion came, and what wasleft was the dregs. Nobody wanted what was left. Well, there was no useeating with them!
Over on the other side of the dining hall wasa chemistry table. I had worked with one of the fellows, Dave McCall;furthermore he was courting our secretary at the time. I went over andsaid, ``Do you mind if I join you?‘‘ They can‘t say no, so I startedeating with them for a while. And I started asking, ``What are theimportant problems of your field?‘‘ And after a week or so, ``Whatimportant problems are you working on?‘‘ And after some more time Icame in one day and said, ``If what you are doing is not important, andif you don‘t think it is going to lead to something important, why areyou at Bell Labs working on it?‘‘ I wasn‘t welcomed after that; I hadto find somebody else to eat with! That was in the spring.
Inthe fall, Dave McCall stopped me in the hall and said, ``Hamming, thatremark of yours got underneath my skin. I thought about it all summer,i.e. what were the important problems in my field. I haven‘t changed myresearch,‘‘ he says, ``but I think it was well worthwhile.‘‘ And Isaid, ``Thank you Dave,‘‘ and went on. I noticed a couple of monthslater he was made the head of the department. I noticed the other dayhe was a Member of the National Academy of Engineering. I noticed hehas succeeded. I have never heard the names of any of the other fellowsat that table mentioned in science and scientific circles. They wereunable to ask themselves, ``What are the important problems in myfield?‘‘
If you do not work on an important problem, it‘sunlikely you‘ll do important work. It‘s perfectly obvious. Greatscientists have thought through, in a careful way, a number ofimportant problems in their field, and they keep an eye on wonderinghow to attack them. Let me warn you, `important problem‘ must bephrased carefully. The three outstanding problems in physics, in acertain sense, were never worked on while I was at Bell Labs. Byimportant I mean guaranteed a Nobel Prize and any sum of money you wantto mention. We didn‘t work on (1) time travel, (2) teleportation, and(3) antigravity. They are not important problems because we do not havean attack. It‘s not the consequence that makes a problem important, itis that you have a reasonable attack. That is what makes a problemimportant. When I say that most scientists don‘t work on importantproblems, I mean it in that sense. The average scientist, so far as Ican make out, spends almost all his time working on problems which hebelieves will not be important and he also doesn‘t believe that theywill lead to important problems.
I spoke earlier about plantingacorns so that oaks will grow. You can‘t always know exactly where tobe, but you can keep active in places where something might happen. Andeven if you believe that great science is a matter of luck, you canstand on a mountain top where lightning strikes; you don‘t have to hidein the valley where you‘re safe. But the average scientist does routinesafe work almost all the time and so he (or she) doesn‘t produce much.It‘s that simple. If you want to do great work, you clearly must workon important problems, and you should have an idea.
Along thoselines at some urging from John Tukey and others, I finally adopted whatI called ``Great Thoughts Time.‘‘ When I went to lunch Friday noon, Iwould only discuss great thoughts after that. By great thoughts I meanones like: ``What will be the role of computers in all of AT&T?‘‘,``How will computers change science?‘‘ For example, I came up with theobservation at that time that nine out of ten experiments were done inthe lab and one in ten on the computer. I made a remark to the vicepresidents one time, that it would be reversed, i.e. nine out of tenexperiments would be done on the computer and one in ten in the lab.They knew I was a crazy mathematician and had no sense of reality. Iknew they were wrong and they‘ve been proved wrong while I have beenproved right. They built laboratories when they didn‘t need them. I sawthat computers were transforming science because I spent a lot of timeasking ``What will be the impact of computers on science and how can Ichange it?‘‘ I asked myself, ``How is it going to change Bell Labs?‘‘ Iremarked one time, in the same address, that more than one-half of thepeople at Bell Labs will be interacting closely with computing machinesbefore I leave. Well, you all have terminals now. I thought hard aboutwhere was my field going, where were the opportunities, and what werethe important things to do. Let me go there so there is a chance I cando important things.
Most great scientists know many importantproblems. They have something between 10 and 20 important problems forwhich they are looking for an attack. And when they see a new idea comeup, one hears them say ``Well that bears on this problem.‘‘ They dropall the other things and get after it. Now I can tell you a horrorstory that was told to me but I can‘t vouch for the truth of it. I wassitting in an airport talking to a friend of mine from Los Alamos abouthow it was lucky that the fission experiment occurred over in Europewhen it did because that got us working on the atomic bomb here in theUS. He said ``No; at Berkeley we had gathered a bunch of data; wedidn‘t get around to reducing it because we were building some moreequipment, but if we had reduced that data we would have foundfission.‘‘ They had it in their hands and they didn‘t pursue it. Theycame in second!
The great scientists, when an opportunity opensup, get after it and they pursue it. They drop all other things. Theyget rid of other things and they get after an idea because they hadalready thought the thing through. Their minds are prepared; they seethe opportunity and they go after it. Now of course lots of times itdoesn‘t work out, but you don‘t have to hit many of them to do somegreat science. It‘s kind of easy. One of the chief tricks is to live along time!
Another trait, it took me a while to notice. Inoticed the following facts about people who work with the door open orthe door closed. I notice that if you have the door to your officeclosed, you get more work done today and tomorrow, and you are moreproductive than most. But 10 years later somehow you don‘t know quiteknow what problems are worth working on; all the hard work you do issort of tangential in importance. He who works with the door open getsall kinds of interruptions, but he also occasionally gets clues as towhat the world is and what might be important. Now I cannot prove thecause and effect sequence because you might say, ``The closed door issymbolic of a closed mind.‘‘ I don‘t know. But I can say there is apretty good correlation between those who work with the doors open andthose who ultimately do important things, although people who work withdoors closed often work harder. Somehow they seem to work on slightlythe wrong thing - not much, but enough that they miss fame.
Iwant to talk on another topic. It is based on the song which I thinkmany of you know, ``It ain‘t what you do, it‘s the way that you doit.‘‘ I‘ll start with an example of my own. I was conned into doing ona digital computer, in the absolute binary days, a problem which thebest analog computers couldn‘t do. And I was getting an answer. When Ithought carefully and said to myself, ``You know, Hamming, you‘re goingto have to file a report on this military job; after you spend a lot ofmoney you‘re going to have to account for it and every analoginstallation is going to want the report to see if they can‘t findflaws in it.‘‘ I was doing the required integration by a rather crummymethod, to say the least, but I was getting the answer. And I realizedthat in truth the problem was not just to get the answer; it was todemonstrate for the first time, and beyond question, that I could beatthe analog computer on its own ground with a digital machine. Ireworked the method of solution, created a theory which was nice andelegant, and changed the way we computed the answer; the results wereno different. The published report had an elegant method which waslater known for years as ``Hamming‘s Method of Integrating DifferentialEquations.‘‘ It is somewhat obsolete now, but for a while it was a verygood method. By changing the problem slightly, I did important workrather than trivial work.
In the same way, when using themachine up in the attic in the early days, I was solving one problemafter another after another; a fair number were successful and therewere a few failures. I went home one Friday after finishing a problem,and curiously enough I wasn‘t happy; I was depressed. I could see lifebeing a long sequence of one problem after another after another. Afterquite a while of thinking I decided, ``No, I should be in the massproduction of a variable product. I should be concerned with all ofnext year‘s problems, not just the one in front of my face.‘‘ Bychanging the question I still got the same kind of results or better,but I changed things and did important work. I attacked the majorproblem - How do I conquer machines and do all of next year‘s problemswhen I don‘t know what they are going to be? How do I prepare for it?How do I do this one so I‘ll be on top of it? How do I obey Newton‘srule? He said, ``If I have seen further than others, it is because I‘vestood on the shoulders of giants.‘‘ These days we stand on each other‘sfeet!
You should do your job in such a fashion that others canbuild on top of it, so they will indeed say, ``Yes, I‘ve stood on soand so‘s shoulders and I saw further.‘‘ The essence of science iscumulative. By changing a problem slightly you can often do great workrather than merely good work. Instead of attacking isolated problems, Imade the resolution that I would never again solve an isolated problemexcept as characteristic of a class.
Now if you are much of amathematician you know that the effort to generalize often means thatthe solution is simple. Often by stopping and saying, ``This is theproblem he wants but this is characteristic of so and so. Yes, I canattack the whole class with a far superior method than the particularone because I was earlier embedded in needless detail.‘‘ The businessof abstraction frequently makes things simple. Furthermore, I filedaway the methods and prepared for the future problems.
To endthis part, I‘ll remind you, ``It is a poor workman who blames his tools- the good man gets on with the job, given what he‘s got, and gets thebest answer he can.‘‘ And I suggest that by altering the problem, bylooking at the thing differently, you can make a great deal ofdifference in your final productivity because you can either do it insuch a fashion that people can indeed build on what you‘ve done, or youcan do it in such a fashion that the next person has to essentiallyduplicate again what you‘ve done. It isn‘t just a matter of the job,it‘s the way you write the report, the way you write the paper, thewhole attitude. It‘s just as easy to do a broad, general job as onevery special case. And it‘s much more satisfying and rewarding!
Ihave now come down to a topic which is very distasteful; it is notsufficient to do a job, you have to sell it. `Selling‘ to a scientistis an awkward thing to do. It‘s very ugly; you shouldn‘t have to do it.The world is supposed to be waiting, and when you do something great,they should rush out and welcome it. But the fact is everyone is busywith their own work. You must present it so well that they will setaside what they are doing, look at what you‘ve done, read it, and comeback and say, ``Yes, that was good.‘‘ I suggest that when you open ajournal, as you turn the pages, you ask why you read some articles andnot others. You had better write your report so when it is published inthe Physical Review, or wherever else you want it, as the readers areturning the pages they won‘t just turn your pages but they will stopand read yours. If they don‘t stop and read it, you won‘t get credit.
Thereare three things you have to do in selling. You have to learn to writeclearly and well so that people will read it, you must learn to givereasonably formal talks, and you also must learn to give informaltalks. We had a lot of so-called `back room scientists.‘ In aconference, they would keep quiet. Three weeks later after a decisionwas made they filed a report saying why you should do so and so. Well,it was too late. They would not stand up right in the middle of a hotconference, in the middle of activity, and say, ``We should do this forthese reasons.‘‘ You need to master that form of communication as wellas prepared speeches.
When I first started, I got practicallyphysically ill while giving a speech, and I was very, very nervous. Irealized I either had to learn to give speeches smoothly or I wouldessentially partially cripple my whole career. The first time IBM askedme to give a speech in New York one evening, I decided I was going togive a really good speech, a speech that was wanted, not a technicalone but a broad one, and at the end if they liked it, I‘d quietly say,``Any time you want one I‘ll come in and give you one.‘‘ As a result, Igot a great deal of practice giving speeches to a limited audience andI got over being afraid. Furthermore, I could also then study whatmethods were effective and what were ineffective.
While going tomeetings I had already been studying why some papers are remembered andmost are not. The technical person wants to give a highly limitedtechnical talk. Most of the time the audience wants a broad generaltalk and wants much more survey and background than the speaker iswilling to give. As a result, many talks are ineffective. The speakernames a topic and suddenly plunges into the details he‘s solved. Fewpeople in the audience may follow. You should paint a general pictureto say why it‘s important, and then slowly give a sketch of what wasdone. Then a larger number of people will say, ``Yes, Joe has donethat,‘‘ or ``Mary has done that; I really see where it is; yes, Maryreally gave a good talk; I understand what Mary has done.‘‘ Thetendency is to give a highly restricted, safe talk; this is usuallyineffective. Furthermore, many talks are filled with far too muchinformation. So I say this idea of selling is obvious.
Let mesummarize. You‘ve got to work on important problems. I deny that it isall luck, but I admit there is a fair element of luck. I subscribe toPasteur‘s ``Luck favors the prepared mind.‘‘ I favor heavily what Idid. Friday afternoons for years - great thoughts only - means that Icommitted 10% of my time trying to understand the bigger problems inthe field, i.e. what was and what was not important. I found in theearly days I had believed `this‘ and yet had spent all week marching in`that‘ direction. It was kind of foolish. If I really believe theaction is over there, why do I march in this direction? I either had tochange my goal or change what I did. So I changed something I did and Imarched in the direction I thought was important. It‘s that easy.
Nowyou might tell me you haven‘t got control over what you have to workon. Well, when you first begin, you may not. But once you‘re moderatelysuccessful, there are more people asking for results than you candeliver and you have some power of choice, but not completely. I‘lltell you a story about that, and it bears on the subject of educatingyour boss. I had a boss named Schelkunoff; he was, and still is, a verygood friend of mine. Some military person came to me and demanded someanswers by Friday. Well, I had already dedicated my computing resourcesto reducing data on the fly for a group of scientists; I was knee deepin short, small, important problems. This military person wanted me tosolve his problem by the end of the day on Friday. I said, ``No, I‘llgive it to you Monday. I can work on it over the weekend. I‘m not goingto do it now.‘‘ He goes down to my boss, Schelkunoff, and Schelkunoffsays, ``You must run this for him; he‘s got to have it by Friday.‘‘ Itell him, ``Why do I?‘‘; he says, ``You have to.‘‘ I said, ``Fine,Sergei, but you‘re sitting in your office Friday afternoon catching thelate bus home to watch as this fellow walks out that door.‘‘ I gave themilitary person the answers late Friday afternoon. I then went toSchelkunoff‘s office and sat down; as the man goes out I say, ``You seeSchelkunoff, this fellow has nothing under his arm; but I gave him theanswers.‘‘ On Monday morning Schelkunoff called him up and said, ``Didyou come in to work over the weekend?‘‘ I could hear, as it were, apause as the fellow ran through his mind of what was going to happen;but he knew he would have had to sign in, and he‘d better not say hehad when he hadn‘t, so he said he hadn‘t. Ever after that Schelkunoffsaid, ``You set your deadlines; you can change them.‘‘
Onelesson was sufficient to educate my boss as to why I didn‘t want to dobig jobs that displaced exploratory research and why I was justified innot doing crash jobs which absorb all the research computingfacilities. I wanted instead to use the facilities to compute a largenumber of small problems. Again, in the early days, I was limited incomputing capacity and it was clear, in my area, that a ``mathematicianhad no use for machines.‘‘ But I needed more machine capacity. Everytime I had to tell some scientist in some other area, ``No I can‘t; Ihaven‘t the machine capacity,‘‘ he complained. I said ``Go tell yourVice President that Hamming needs more computing capacity.‘‘ After awhile I could see what was happening up there at the top; many peoplesaid to my Vice President, ``Your man needs more computing capacity.‘‘I got it!
I also did a second thing. When I loaned what littleprogramming power we had to help in the early days of computing, Isaid, ``We are not getting the recognition for our programmers thatthey deserve. When you publish a paper you will thank that programmeror you aren‘t getting any more help from me. That programmer is goingto be thanked by name; she‘s worked hard.‘‘ I waited a couple of years.I then went through a year of BSTJ articles and counted what fractionthanked some programmer. I took it into the boss and said, ``That‘s thecentral role computing is playing in Bell Labs; if the BSTJ isimportant, that‘s how important computing is.‘‘ He had to give in. Youcan educate your bosses. It‘s a hard job. In this talk I‘m only viewingfrom the bottom up; I‘m not viewing from the top down. But I am tellingyou how you can get what you want in spite of top management. You haveto sell your ideas there also.
Well I now come down to thetopic, ``Is the effort to be a great scientist worth it?‘‘ To answerthis, you must ask people. When you get beyond their modesty, mostpeople will say, ``Yes, doing really first-class work, and knowing it,is as good as wine, women and song put together,‘‘ or if it‘s a womanshe says, ``It is as good as wine, men and song put together.‘‘ And ifyou look at the bosses, they tend to come back or ask for reports,trying to participate in those moments of discovery. They‘re always inthe way. So evidently those who have done it, want to do it again. Butit is a limited survey. I have never dared to go out and ask those whodidn‘t do great work how they felt about the matter. It‘s a biasedsample, but I still think it is worth the struggle. I think it is verydefinitely worth the struggle to try and do first-class work becausethe truth is, the value is in the struggle more than it is in theresult. The struggle to make something of yourself seems to beworthwhile in itself. The success and fame are sort of dividends, in myopinion.
I‘ve told you how to do it. It is so easy, so why do somany people, with all their talents, fail? For example, my opinion, tothis day, is that there are in the mathematics department at Bell Labsquite a few people far more able and far better endowed than I, butthey didn‘t produce as much. Some of them did produce more than I did;Shannon produced more than I did, and some others produced a lot, but Iwas highly productive against a lot of other fellows who were betterequipped. Why is it so? What happened to them? Why do so many of thepeople who have great promise, fail?
Well, one of the reasons isdrive and commitment. The people who do great work with less abilitybut who are committed to it, get more done that those who have greatskill and dabble in it, who work during the day and go home and doother things and come back and work the next day. They don‘t have thedeep commitment that is apparently necessary for really first-classwork. They turn out lots of good work, but we were talking, remember,about first-class work. There is a difference. Good people, verytalented people, almost always turn out good work. We‘re talking aboutthe outstanding work, the type of work that gets the Nobel Prize andgets recognition.
The second thing is, I think, the problem ofpersonality defects. Now I‘ll cite a fellow whom I met out in Irvine.He had been the head of a computing center and he was temporarily onassignment as a special assistant to the president of the university.It was obvious he had a job with a great future. He took me into hisoffice one time and showed me his method of getting letters done andhow he took care of his correspondence. He pointed out how inefficientthe secretary was. He kept all his letters stacked around there; heknew where everything was. And he would, on his word processor, get theletter out. He was bragging how marvelous it was and how he could getso much more work done without the secretary‘s interference. Well,behind his back, I talked to the secretary. The secretary said, ``Ofcourse I can‘t help him; I don‘t get his mail. He won‘t give me thestuff to log in; I don‘t know where he puts it on the floor. Of courseI can‘t help him.‘‘ So I went to him and said, ``Look, if you adopt thepresent method and do what you can do single-handedly, you can go justthat far and no farther than you can do single-handedly. If you willlearn to work with the system, you can go as far as the system willsupport you.‘‘ And, he never went any further. He had his personalitydefect of wanting total control and was not willing to recognize thatyou need the support of the system.
You find this happeningagain and again; good scientists will fight the system rather thanlearn to work with the system and take advantage of all the system hasto offer. It has a lot, if you learn how to use it. It takes patience,but you can learn how to use the system pretty well, and you can learnhow to get around it. After all, if you want a decision `No‘, you justgo to your boss and get a `No‘ easy. If you want to do something, don‘task, do it. Present him with an accomplished fact. Don‘t give him achance to tell you `No‘. But if you want a `No‘, it‘s easy to get a`No‘.
Another personality defect is ego assertion and I‘ll speakin this case of my own experience. I came from Los Alamos and in theearly days I was using a machine in New York at 590 Madison Avenuewhere we merely rented time. I was still dressing in western clothes,big slash pockets, a bolo and all those things. I vaguely noticed thatI was not getting as good service as other people. So I set out tomeasure. You came in and you waited for your turn; I felt I was notgetting a fair deal. I said to myself, ``Why? No Vice President at IBMsaid, `Give Hamming a bad time‘. It is the secretaries at the bottomwho are doing this. When a slot appears, they‘ll rush to find someoneto slip in, but they go out and find somebody else. Now, why? I haven‘tmistreated them.‘‘ Answer, I wasn‘t dressing the way they felt somebodyin that situation should. It came down to just that - I wasn‘t dressingproperly. I had to make the decision - was I going to assert my ego anddress the way I wanted to and have it steadily drain my effort from myprofessional life, or was I going to appear to conform better? (道)Idecided I would make an effort to appear to conform properly. Themoment I did, I got much better service. And now, as an old colorfulcharacter, I get better service than other people.
You shoulddress according to the expectations of the audience spoken to. If I amgoing to give an address at the MIT computer center, I dress with abolo and an old corduroy jacket or something else. I know enough not tolet my clothes, my appearance, my manners get in the way of what I careabout. An enormous number of scientists feel they must assert their egoand do their thing their way. They have got to be able to do this,that, or the other thing, and they pay a steady price.
JohnTukey almost always dressed very casually. He would go into animportant office and it would take a long time before the other fellowrealized that this is a first-class man and he had better listen. For along time John has had to overcome this kind of hostility. It‘s wastedeffort! I didn‘t say you should conform; I said ``The appearance ofconforming gets you a long way.‘‘ If you chose to assert your ego inany number of ways, ``I am going to do it my way,‘‘ you pay a smallsteady price throughout the whole of your professional career. Andthis, over a whole lifetime, adds up to an enormous amount of needlesstrouble.
By taking the trouble to tell jokes to the secretariesand being a little friendly, I got superb secretarial help. Forinstance, one time for some idiot reason all the reproducing servicesat Murray Hill were tied up. Don‘t ask me how, but they were. I wantedsomething done. My secretary called up somebody at Holmdel, hopped thecompany car, made the hour-long trip down and got it reproduced, andthen came back. It was a payoff for the times I had made an effort tocheer her up, tell her jokes and be friendly; it was that little extrawork that later paid off for me. By realizing you have to use thesystem and studying how to get the system to do your work, you learnhow to adapt the system to your desires. Or you can fight it steadily,as a small undeclared war, for the whole of your life.
And Ithink John Tukey paid a terrible price needlessly. He was a geniusanyhow, but I think it would have been far better, and far simpler, hadhe been willing to conform a little bit instead of ego asserting. He isgoing to dress the way he wants all of the time. It applies not only todress but to a thousand other things; people will continue to fight thesystem. Not that you shouldn‘t occasionally!
When they moved thelibrary from the middle of Murray Hill to the far end, a friend of mineput in a request for a bicycle. Well, the organization was not dumb.They waited awhile and sent back a map of the grounds saying, ``Willyou please indicate on this map what paths you are going to take so wecan get an insurance policy covering you.‘‘ A few more weeks went by.They then asked, ``Where are you going to store the bicycle and howwill it be locked so we can do so and so.‘‘ He finally realized that ofcourse he was going to be red-taped to death so he gave in. He rose tobe the President of Bell Laboratories.
Barney Oliver was a goodman. He wrote a letter one time to the IEEE. At that time the officialshelf space at Bell Labs was so much and the height of the IEEEProceedings at that time was larger; and since you couldn‘t change thesize of the official shelf space he wrote this letter to the IEEEPublication person saying, ``Since so many IEEE members were at BellLabs and since the official space was so high the journal size shouldbe changed.‘‘ He sent it for his boss‘s signature. Back came a carbonwith his signature, but he still doesn‘t know whether the original wassent or not. I am not saying you shouldn‘t make gestures of reform. Iam saying that my study of able people is that they don‘t getthemselves committed to that kind of warfare. They play it a little bitand drop it and get on with their work.
Many a second-ratefellow gets caught up in some little twitting of the system, andcarries it through to warfare. He expends his energy in a foolishproject. Now you are going to tell me that somebody has to change thesystem. I agree; somebody‘s has to. Which do you want to be? The personwho changes the system or the person who does first-class science?Which person is it that you want to be? Be clear, when you fight thesystem and struggle with it, what you are doing, how far to go out ofamusement, and how much to waste your effort fighting the system. Myadvice is to let somebody else do it and you get on with becoming afirst-class scientist. Very few of you have the ability to both reformthe system and become a first-class scientist.
On the otherhand, we can‘t always give in. There are times when a certain amount ofrebellion is sensible. I have observed almost all scientists enjoy acertain amount of twitting the system for the sheer love of it. What itcomes down to basically is that you cannot be original in one areawithout having originality in others. Originality is being different.You can‘t be an original scientist without having some other originalcharacteristics. But many a scientist has let his quirks in otherplaces make him pay a far higher price than is necessary for the egosatisfaction he or she gets. I‘m not against all ego assertion; I‘magainst some.
Another fault is anger. Often a scientist becomesangry, and this is no way to handle things. Amusement, yes, anger, no.Anger is misdirected. You should follow and cooperate rather thanstruggle against the system all the time.
Another thing youshould look for is the positive side of things instead of the negative.I have already given you several examples, and there are many, manymore; how, given the situation, by changing the way I looked at it, Iconverted what was apparently a defect to an asset. I‘ll give youanother example. I am an egotistical person; there is no doubt aboutit. I knew that most people who took a sabbatical to write a book,didn‘t finish it on time. So before I left, I told all my friends thatwhen I come back, that book was going to be done! Yes, I would have itdone - I‘d have been ashamed to come back without it! I used my ego tomake myself behave the way I wanted to. I bragged about something soI‘d have to perform. I found out many times, like a cornered rat in areal trap, I was surprisingly capable. I have found that it paid tosay, ``Oh yes, I‘ll get the answer for you Tuesday,‘‘ not having anyidea how to do it. By Sunday night I was really hard thinking on how Iwas going to deliver by Tuesday. I often put my pride on the line andsometimes I failed, but as I said, like a cornered rat I‘m surprisedhow often I did a good job. I think you need to learn to use yourself.I think you need to know how to convert a situation from one view toanother which would increase the chance of success.
Nowself-delusion in humans is very, very common. There are enumerable waysof you changing a thing and kidding yourself and making it look someother way. When you ask, ``Why didn‘t you do such and such,‘‘ theperson has a thousand alibis. If you look at the history of science,usually these days there are 10 people right there ready, and we payoff for the person who is there first. The other nine fellows say,``Well, I had the idea but I didn‘t do it and so on and so on.‘‘ Thereare so many alibis. Why weren‘t you first? Why didn‘t you do it right?Don‘t try an alibi. Don‘t try and kid yourself. You can tell otherpeople all the alibis you want. I don‘t mind. But to yourself try to behonest.
If you really want to be a first-class scientist youneed to know yourself, your weaknesses, your strengths, and your badfaults, like my egotism. How can you convert a fault to an asset? Howcan you convert a situation where you haven‘t got enough manpower tomove into a direction when that‘s exactly what you need to do? I sayagain that I have seen, as I studied the history, the successfulscientist changed the viewpoint and what was a defect became an asset.
Insummary, I claim that some of the reasons why so many people who havegreatness within their grasp don‘t succeed are: they don‘t work onimportant problems, they don‘t become emotionally involved, they don‘ttry and change what is difficult to some other situation which iseasily done but is still important, and they keep giving themselvesalibis why they don‘t. They keep saying that it is a matter of luck.I‘ve told you how easy it is; furthermore I‘ve told you how to reform.Therefore, go forth and become great scientists!
Questions and Answers
A.G. Chynoweth: Well that was 50 minutes of concentrated wisdom andobservations accumulated over a fantastic career; I lost track of allthe observations that were striking home. Some of them are very verytimely. One was the plea for more computer capacity; I was hearingnothing but that this morning from several people, over and over again.So that was right on the mark today even though here we are 20 - 30years after when you were making similar remarks, Dick. I can think ofall sorts of lessons that all of us can draw from your talk. And forone, as I walk around the halls in the future I hope I won‘t see asmany closed doors in Bellcore. That was one observation I thought wasvery intriguing.
Thank you very, very much indeed Dick; that wasa wonderful recollection. I‘ll now open it up for questions. I‘m surethere are many people who would like to take up on some of the pointsthat Dick was making.
Hamming: First let me respond to AlanChynoweth about computing. I had computing in research and for 10 yearsI kept telling my management, ``Get that !&@#% machine out ofresearch. We are being forced to run problems all the time. We can‘t doresearch because were too busy operating and running the computingmachines.‘‘ Finally the message got through. They were going to movecomputing out of research to someplace else. I was persona non grata tosay the least and I was surprised that people didn‘t kick my shinsbecause everybody was having their toy taken away from them. I went into Ed David‘s office and said, ``Look Ed, you‘ve got to give yourresearchers a machine. If you give them a great big machine, we‘ll beback in the same trouble we were before, so busy keeping it going wecan‘t think. Give them the smallest machine you can because they arevery able people. They will learn how to do things on a small machineinstead of mass computing.‘‘ As far as I‘m concerned, that‘s how UNIXarose. We gave them a moderately small machine and they decided to makeit do great things. They had to come up with a system to do it on. Itis called UNIX!
A. G. Chynoweth: I just have to pick up on thatone. In our present environment, Dick, while we wrestle with some ofthe red tape attributed to, or required by, the regulators, there isone quote that one exasperated AVP came up with and I‘ve used it overand over again. He growled that, ``UNIX was never a deliverable!‘‘
Question: What about personal stress? Does that seem to make a difference?
Hamming:Yes, it does. If you don‘t get emotionally involved, it doesn‘t. I hadincipient ulcers most of the years that I was at Bell Labs. I havesince gone off to the Naval Postgraduate School and laid back somewhat,and now my health is much better. But if you want to be a greatscientist you‘re going to have to put up with stress. You can lead anice life; you can be a nice guy or you can be a great scientist. Butnice guys end last, is what Leo Durocher said. If you want to lead anice happy life with a lot of recreation and everything else, you‘lllead a nice life.
Question: The remarks about having courage, noone could argue with; but those of us who have gray hairs or who arewell established don‘t have to worry too much. But what I sense amongthe young people these days is a real concern over the risk taking in ahighly competitive environment. Do you have any words of wisdom on this?
Hamming:I‘ll quote Ed David more. Ed David was concerned about the general lossof nerve in our society. It does seem to me that we‘ve gone throughvarious periods. Coming out of the war, coming out of Los Alamos wherewe built the bomb, coming out of building the radars and so on, therecame into the mathematics department, and the research area, a group ofpeople with a lot of guts. They‘ve just seen things done; they‘ve justwon a war which was fantastic. We had reasons for having courage andtherefore we did a great deal. I can‘t arrange that situation to do itagain. I cannot blame the present generation for not having it, but Iagree with what you say; I just cannot attach blame to it. It doesn‘tseem to me they have the desire for greatness; they lack the courage todo it. But we had, because we were in a favorable circumstance to haveit; we just came through a tremendously successful war. In the war wewere looking very, very bad for a long while; it was a very desperatestruggle as you well know. And our success, I think, gave us courageand self confidence; that‘s why you see, beginning in the late fortiesthrough the fifties, a tremendous productivity at the labs which wasstimulated from the earlier times. Because many of us were earlierforced to learn other things - we were forced to learn the things wedidn‘t want to learn, we were forced to have an open door - and then wecould exploit those things we learned. It is true, and I can‘t doanything about it; I cannot blame the present generation either. It‘sjust a fact.
Question: Is there something management could or should do?
Hamming:Management can do very little. If you want to talk about managingresearch, that‘s a totally different talk. I‘d take another hour doingthat. This talk is about how the individual gets very successfulresearch done in spite of anything the management does or in spite ofany other opposition. And how do you do it? Just as I observe peopledoing it. It‘s just that simple and that hard!
Question: Is brainstorming a daily process?
Hamming:Once that was a very popular thing, but it seems not to have paid off.For myself I find it desirable to talk to other people; but a sessionof brainstorming is seldom worthwhile. I do go in to strictly talk tosomebody and say, ``Look, I think there has to be something here.Here‘s what I think I see ...‘‘ and then begin talking back and forth.But you want to pick capable people. To use another analogy, you knowthe idea called the `critical mass.‘ If you have enough stuff you havecritical mass. There is also the idea I used to call `sound absorbers‘.When you get too many sound absorbers, you give out an idea and theymerely say, ``Yes, yes, yes.‘‘ What you want to do is get that criticalmass in action; ``Yes, that reminds me of so and so,‘‘ or, ``Have youthought about that or this?‘‘ When you talk to other people, you wantto get rid of those sound absorbers who are nice people but merely say,``Oh yes,‘‘ and to find those who will stimulate you right back.
Forexample, you couldn‘t talk to John Pierce without being stimulated veryquickly. There were a group of other people I used to talk with. Forexample there was Ed Gilbert; I used to go down to his office regularlyand ask him questions and listen and come back stimulated. I picked mypeople carefully with whom I did or whom I didn‘t brainstorm becausethe sound absorbers are a curse. They are just nice guys; they fill thewhole space and they contribute nothing except they absorb ideas andthe new ideas just die away instead of echoing on. Yes, I find itnecessary to talk to people. I think people with closed doors fail todo this so they fail to get their ideas sharpened, such as ``Did youever notice something over here?‘‘ I never knew anything about it - Ican go over and look. Somebody points the way. On my visit here, I havealready found several books that I must read when I get home. I talk topeople and ask questions when I think they can answer me and give meclues that I do not know about. I go out and look!
Question: What kind of tradeoffs did you make in allocating your time for reading and writing and actually doing research?
Hamming:I believed, in my early days, that you should spend at least as muchtime in the polish and presentation as you did in the originalresearch. Now at least 50% of the time must go for the presentation.It‘s a big, big number.
Question: How much effort should go into library work?
Hamming:It depends upon the field. I will say this about it. There was a fellowat Bell Labs, a very, very, smart guy. He was always in the library; heread everything. If you wanted references, you went to him and he gaveyou all kinds of references. But in the middle of forming thesetheories, I formed a proposition: there would be no effect named afterhim in the long run. He is now retired from Bell Labs and is an AdjunctProfessor. He was very valuable; I‘m not questioning that. He wrotesome very good Physical Review articles; but there‘s no effect namedafter him because he read too much. If you read all the time what otherpeople have done you will think the way they thought. If you want tothink new thoughts that are different, then do what a lot of creativepeople do - get the problem reasonably clear and then refuse to look atany answers until you‘ve thought the problem through carefully how youwould do it, how you could slightly change the problem to be thecorrect one. So yes, you need to keep up. You need to keep up more tofind out what the problems are than to read to find the solutions. Thereading is necessary to know what is going on and what is possible. Butreading to get the solutions does not seem to be the way to do greatresearch. So I‘ll give you two answers. You read; but it is not theamount, it is the way you read that counts.
Question: How do you get your name attached to things?
Hamming:By doing great work. I‘ll tell you the hamming window one. I had givenTukey a hard time, quite a few times, and I got a phone call from himfrom Princeton to me at Murray Hill. I knew that he was writing uppower spectra and he asked me if I would mind if he called a certainwindow a ``Hamming window.‘‘ And I said to him, ``Come on, John; youknow perfectly well I did only a small part of the work but you alsodid a lot.‘‘ He said, ``Yes, Hamming, but you contributed a lot ofsmall things; you‘re entitled to some credit.‘‘ So he called it thehamming window. Now, let me go on. I had twitted John frequently abouttrue greatness. I said true greatness is when your name is like ampere,watt, and fourier - when it‘s spelled with a lower case letter. That‘show the hamming window came about.
Question: Dick, would you care to comment on the relative effectiveness between giving talks, writing papers, and writing books?
Hamming:In the short-haul, papers are very important if you want to stimulatesomeone tomorrow. If you want to get recognition long-haul, it seems tome writing books is more contribution because most of us needorientation. In this day of practically infinite knowledge, we needorientation to find our way. Let me tell you what infinite knowledgeis. Since from the time of Newton to now, we have come close todoubling knowledge every 17 years, more or less. And we cope with that,essentially, by specialization. In the next 340 years at that rate,there will be 20 doublings, i.e. a million, and there will be a millionfields of specialty for every one field now. It isn‘t going to happen.The present growth of knowledge will choke itself off until we getdifferent tools. I believe that books which try to digest, coordinate,get rid of the duplication, get rid of the less fruitful methods andpresent the underlying ideas clearly of what we know now, will be thethings the future generations will value. Public talks are necessary;private talks are necessary; written papers are necessary. But I aminclined to believe that, in the long-haul, books which leave outwhat‘s not essential are more important than books which tell youeverything because you don‘t want to know everything. I don‘t want toknow that much about penguins is the usual reply. You just want to knowthe essence.
Question: You mentioned the problem of the NobelPrize and the subsequent notoriety of what was done to some of thecareers. Isn‘t that kind of a much more broad problem of fame? What canone do?
Hamming: Some things you could do are the following.Somewhere around every seven years make a significant, if not complete,shift in your field. Thus, I shifted from numerical analysis, tohardware, to software, and so on, periodically, because you tend to useup your ideas. When you go to a new field, you have to start over as ababy. You are no longer the big mukity muk and you can start back thereand you can start planting those acorns which will become the giantoaks. Shannon, I believe, ruined himself. In fact when he left BellLabs, I said, ``That‘s the end of Shannon‘s scientific career.‘‘ Ireceived a lot of flak from my friends who said that Shannon was justas smart as ever. I said, ``Yes, he‘ll be just as smart, but that‘s theend of his scientific career,‘‘ and I truly believe it was.
Youhave to change. You get tired after a while; you use up youroriginality in one field. You need to get something nearby. I‘m notsaying that you shift from music to theoretical physics to Englishliterature; I mean within your field you should shift areas so that youdon‘t go stale. You couldn‘t get away with forcing a change every sevenyears, but if you could, I would require a condition for doingresearch, being that you will change your field of research every sevenyears with a reasonable definition of what it means, or at the end of10 years, management has the right to compel you to change. I wouldinsist on a change because I‘m serious. What happens to the old fellowsis that they get a technique going; they keep on using it. They weremarching in that direction which was right then, but the world changes.There‘s the new direction; but the old fellows are still marching intheir former direction.
You need to get into a new field to getnew viewpoints, and before you use up all the old ones. You can dosomething about this, but it takes effort and energy. It takes courageto say, ``Yes, I will give up my great reputation.‘‘ For example, whenerror correcting codes were well launched, having these theories, Isaid, ``Hamming, you are going to quit reading papers in the field; youare going to ignore it completely; you are going to try and dosomething else other than coast on that.‘‘ I deliberately refused to goon in that field. I wouldn‘t even read papers to try to force myself tohave a chance to do something else. I managed myself, which is what I‘mpreaching in this whole talk. Knowing many of my own faults, I managemyself. I have a lot of faults, so I‘ve got a lot of problems, i.e. alot of possibilities of management.
Question: Would you compare research and management?
Hamming:If you want to be a great researcher, you won‘t make it being presidentof the company. If you want to be president of the company, that‘sanother thing. I‘m not against being president of the company. I justdon‘t want to be. I think Ian Ross does a good job as President of BellLabs. I‘m not against it; but you have to be clear on what you want.Furthermore, when you‘re young, you may have picked wanting to be agreat scientist, but as you live longer, you may change your mind. Forinstance, I went to my boss, Bode, one day and said, ``Why did you everbecome department head? Why didn‘t you just be a good scientist?‘‘ Hesaid, ``Hamming, I had a vision of what mathematics should be in BellLaboratories. And I saw if that vision was going to be realized, I hadto make it happen; I had to be department head.‘‘ When your vision ofwhat you want to do is what you can do single-handedly, then you shouldpursue it. The day your vision, what you think needs to be done, isbigger than what you can do single-handedly, then you have to movetoward management. And the bigger the vision is, the farther inmanagement you have to go. If you have a vision of what the wholelaboratory should be, or the whole Bell System, you have to get thereto make it happen. You can‘t make it happen from the bottom veryeasily. It depends upon what goals and what desires you have. And asthey change in life, you have to be prepared to change. I chose toavoid management because I preferred to do what I could dosingle-handedly. But that‘s the choice that I made, and it is biased.Each person is entitled to their choice. Keep an open mind. But whenyou do choose a path, for heaven‘s sake be aware of what you have doneand the choice you have made. Don‘t try to do both sides.
Question:How important is one‘s own expectation or how important is it to be ina group or surrounded by people who expect great work from you?
Hamming:At Bell Labs everyone expected good work from me - it was a big help.Everybody expects you to do a good job, so you do, if you‘ve got pride.I think it‘s very valuable to have first-class people around. I soughtout the best people. The moment that physics table lost the bestpeople, I left. The moment I saw that the same was true of thechemistry table, I left. I tried to go with people who had greatability so I could learn from them and who would expect great resultsout of me. By deliberately managing myself, I think I did much betterthan laissez faire.
Question: You, at the outset of your talk,minimized or played down luck; but you seemed also to gloss over thecircumstances that got you to Los Alamos, that got you to Chicago, thatgot you to Bell Laboratories.
Hamming: There was some luck. Onthe other hand I don‘t know the alternate branches. Until you can saythat the other branches would not have been equally or more successful,I can‘t say. Is it luck the particular thing you do? For example, whenI 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 greatwork. No matter what directions came up in the future, this man woulddo great work. And sure enough, he did do great work. It isn‘t that youonly do a little great work at this circumstance and that was luck,there are many opportunities sooner or later. There are a whole pailfull of opportunities, of which, if you‘re in this situation, you seizeone and you‘re great over there instead of over here. There is anelement of luck, yes and no. Luck favors a prepared mind; luck favors aprepared person. It is not guaranteed; I don‘t guarantee success asbeing absolutely certain. I‘d say luck changes the odds, but there issome definite control on the part of the individual.
Go forth, then, and do great work!