You and Your Research

by Dr. Richard W. Hamming
INTRODUCTION OF DR. RICHARD W. HAMMING
As a speaker in the Bell Communications ResearchColloquium Series, Dr. Richard W. Hamming of the Naval PostgraduateSchool in Monterey, California, was introduced by Alan G. Chynoweth,Vice President, Applied Research, Bell Communications Research.
Alan G. Chynoweth: Greetings colleagues, and also to many of our former colleagues fromBell Labs who, I understand, are here to be with us today on what Iregard as a particularly felicitous occasion. It gives me very greatpleasure indeed to introduce to you my old friend and colleague frommany many years back, Richard Hamming, or Dick Hamming as he has alwaysbeen know to all of us.
Dick is one of the all time greats in themathematics and computer science arenas, as I’m sure the audience heredoes not need reminding. He received his early education at theUniversities of Chicago and Nebraska, and got his Ph.D. at Illinois; hethen joined the Los Alamos project during the war. Afterwards, in 1946,he joined Bell Labs. And that is, of course, where I met Dick - when Ijoined Bell Labs in their physics research organization. In those days,we were in the habit of lunching together as a physics group, and forsome reason this strange fellow from mathematics was always pleased tojoin us. We were always happy to have him with us because he brought somany unorthodox ideas and views. Those lunches were stimulating, I canassure you.
While our professional paths have not been veryclose over the years, nevertheless I’ve always recognized Dick in thehalls of Bell Labs and have always had tremendous admiration for whathe was doing. I think the record speaks for itself. It is too long togo through all the details, but let me point out, for example, that hehas written seven books and of those seven books which tell of variousareas of mathematics and computers and coding and information theory,three are already well into their second edition. That is testimonyindeed to the prolific output and the stature of Dick Hamming.
I think I last met him - it must have been aboutten years ago - at a rather curious little conference in Dublin,Ireland where we were both speakers. As always, he was tremendouslyentertaining. Just one more example of the provocative thoughts that hecomes up with: I remember him saying, “There are wavelengths thatpeople cannot see, there are sounds that people cannot hear, and maybecomputers have thoughts that people cannot think.” Well, with DickHamming around, we don’t need a computer. I think that we are in for anextremely entertaining talk.
THE TALK
It’s a pleasure to be here. I doubt if I can liveup to the Introduction. The title of my talk is, “You and YourResearch” It is not about managing research, it is about how youindividually 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 ordinaryrun-of-the-mill research; I’m talking about great research. And for thesake of describing great research I’ll occasionally say Nobel-Prizetype of work. It doesn’t have to gain the Nobel Prize, but I mean thosekinds of things which we perceive are significant things. Relativity,if you want, Shannon’s information theory, any number of outstandingtheories - that’s the kind of thing I’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 isimportant 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 fromone life to the next! Why shouldn’t you do significant things in thisone 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 iswhat I have studied. But so far as I know, and I’ve been told byothers, much of what I say applies to many fields. Outstanding work ischaracterized very much the same way in most fields, but I will confinemyself to science.
In order to get at you individually, I must talkin the first person. I have to get you to drop modesty and say toyourself, “Yes, I would like to do first-class work” Our society frownson 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 setout 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 somethingsignificant.”
In order to get to the second stage, I have todrop modesty and talk in the first person about what I’ve seen, whatI’ve done, and what I’ve heard. I’m going to talk about people, some ofwhom you know, and I trust that when we leave, you won’t quote me assaying some of the things 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 more than onething from a good person. Once in a while a person does only one thingin his whole life, and we’ll talk about that later, but a lot of timesthere is repetition. I claim that luck will not cover everything. And Iwill cite Pasteur who said, “Luck favors the prepared mind.” And Ithink that says it the way I believe it. There is indeed an element ofluck, and no, there isn’t. The prepared mind sooner or later findssomething important and does it. So yes, it is luck. The particularthing you do is luck, but that you do something is not.
For example, when I came to Bell Labs, I sharedan office for a while with Shannon. At the same time he was doinginformation theory, I was doing coding theory. It is suspicious thatthe two of us did it at the same place and at the same time - it was inthe atmosphere. 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 manypeople have it including great scientists, is that usually when theywere young they had independent thoughts and had the courage to pursuethem. For example, Einstein, somewhere around 12 or 14, asked himselfthe question, “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 soundsgood. Most of you in this room probably have more than enough brains todo first-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 in the same way. Itrust he isn’t in the audience, i.e. a fellow named Clogston. I met himwhen I was working on a problem with John Pierce’s group and I didn’tthink 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 Iwould have fired the fellow, but J. R. Pierce was smart and kept himon. Clogston finally did the Clogston cable. After that there was asteady stream of good ideas. One success brought him confidence andcourage.
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 code do?”He then proves that the average code is arbitrarily good, and thattherefore 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 physicistsparticularly worry about. They always are saying that you have got todo it when you are young or you will never do it. Einstein did thingsvery early, and all the quantum mechanic fellows were disgustinglyyoung when they did their best work. Most mathematicians, theoreticalphysicists, and astrophysicists do what we consider their best workwhen they are young. It is not that they don’t do good work in theirold age but what we value most is often what they did early. On theother hand, in music, politics and literature, often what we considertheir best work was done late. I don’t know how whatever field you arein fits this scale, but age has some effect.
But let me say why age seems to have the effectit does. In the first place if you do some good work you will findyourself on all kinds of committees and unable to do any more work. Youmay find yourself as I saw Brattain when he got a Nobel Prize. The daythe prize was announced we all assembled in Arnold Auditorium; allthree 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 could onlywork on great problems.
When you are famous it is hard to work on smallproblems. This is what did Shannon in. After information theory, whatdo you do for an encore? The great scientists often make this error.They fail to continue to plant the little acorns from which the mightyoak trees grow. They try to get the big thing right off. And that isn’tthe way things go. So that is another reason why you find that when youget early recognition it seems to sterilize you. In fact I will giveyou my favorite quotation of many years. The Institute for AdvancedStudy in Princeton, in my opinion, has ruined more good scientists thanany institution has created, judged by what they did before they cameand judged by what they did after. Not that they weren’t goodafterwards, but they were superb before they got there and were onlygood afterwards.
This brings up the subject, out of order perhaps,of working conditions. What most people think are the best workingconditions, are not. Very clearly they are not because people are oftenmost productive when working conditions are bad. One of the bettertimes of the Cambridge Physical Laboratories was when they hadpractically shacks - they did some of the best physics ever.
I give you a story from my own private life.Early on it became evident to me that Bell Laboratories was not goingto give me the conventional acre of programming people to programcomputing machines in absolute binary. It was clear they weren’t goingto. But that was the way everybody did it. I could go to the West Coastand get a job with the airplane companies without any trouble, but theexciting people were at Bell Labs and the fellows out there in theairplane companies were not. I thought for a long while about, “Did Iwant to go or not?” and I wondered how I could get the best of twopossible worlds. I finally said to myself, “Hamming, you think themachines can do practically everything. Why can’t you make them writeprograms?” What appeared at first to me as a defect forced me intoautomatic programming very early. What appears to be a fault, often, bya change of viewpoint, turns out to be one of the greatest assets youcan have. But you are not likely to think that when you first look thething and say, “Gee, I’m never going to get enough programmers, so howcan I ever do any great programming?”
And there are many other stories of the samekind; Grace Hopper has similar ones. I think that if you look carefullyyou will see that often the great scientists, by turning the problemaround 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 observe thatmost great scientists have tremendous drive. I worked for ten yearswith John Tukey at Bell Labs. He had tremendous drive. One day aboutthree or four years after I joined, I discovered that John Tukey wasslightly younger than I was. John was a genius and I clearly was not.Well I went storming into Bode’s office and said, “How can anybody myage know as much as John Tukey does?” He leaned back in his chair, puthis hands behind his head, grinned slightly, and said, “You would besurprised Hamming, how much you would know if you worked as hard as hedid that many years.” I simply slunk out of the office!
What Bode was saying was this: “Knowledge andproductivity are like compound interest.” Given two people ofapproximately the same ability and one person who works ten percentmore than the other, the latter will more than twice outproduce theformer. The more you know, the more you learn; the more you learn, themore you can do; the more you can do, the more the opportunity - it isvery much like compound interest. I don’t want to give you a rate, butit is a very high rate. Given two people with exactly the same ability,the one person who manages day in and day out to get in one more hourof thinking will be tremendously more productive over a lifetime. Itook Bode’s remark to heart; I spent a good deal more of my time forsome years trying to work a bit harder and I found, in fact, I couldget more work done. I don’t like to say it in front of my wife, but Idid sort of neglect her sometimes; I needed to study. You have toneglect things if you intend to get what you want done. There’s noquestion about this.
On this matter of drive Edison says, “Genius is99% perspiration and 1% inspiration.” He may have been exaggerating,but the idea is that solid work, steadily applied, gets yousurprisingly far. The steady application of effort with a little bitmore work, intelligently applied is what does it. That’s thetrouble; drive, misapplied, doesn’t get you anywhere. I’ve oftenwondered why so many of my good friends at Bell Labs who worked as hardor harder than I did, didn’t have so much to show for it. Themisapplication of effort is a very serious matter. Just hard work isnot enough - it must be applied sensibly.
There’s another trait on the side which I want totalk about; that trait is ambiguity. It took me a while to discover itsimportance. Most people like to believe something is or is not true.Great scientists tolerate ambiguity very well. They believe the theoryenough to go ahead; they doubt it enough to notice the errors andfaults 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 toomuch you won’t get started. It requires a lovely balance. But mostgreat scientists are well aware of why their theories are true and theyare also well aware of some slight misfits which don’t quite fit andthey don’t forget it. Darwin writes in his autobiography that he foundit necessary to write down every piece of evidence which appeared tocontradict his beliefs because otherwise they would disappear from hismind. When you find apparent flaws you’ve got to be sensitive and keeptrack of those things, and keep an eye out for how they can beexplained or how the theory can be changed to fit them. Those are oftenthe great contributions. Great contributions are rarely done by addinganother decimal place. It comes down to an emotional commitment. Mostgreat scientists are completely committed to their problem. Those whodon’t become committed seldom produce outstanding, first-class work.
Now again, emotional commitment is not enough. Itis a necessary condition apparently. And I think I can tell you thereason why. Everybody who has studied creativity is driven finally tosaying, “creativity comes out of your subconscious.” Somehow, suddenly,there it is. It just appears. Well, we know very little about thesubconscious; but one thing you are pretty well aware of is that yourdreams also come out of your subconscious. And you’re aware your dreamsare, to a fair extent, a reworking of the experiences of the day. Ifyou are deeply immersed and committed to a topic, day after day afterday, your subconscious has nothing to do but work on your problem. Andso you wake up one morning, or on some afternoon, and there’s theanswer. For those who don’t get committed to their current problem, thesubconscious goofs off on other things and doesn’t produce the bigresult. So the way to manage yourself is that when you have a realimportant problem you don’t let anything else get the center of yourattention - you keep your thoughts on the problem. Keep yoursubconscious starved so it has to work on your problem, so you can sleep peacefully and get the answer in the morning, free.
Now Alan Chynoweth mentioned that I used to eatat the physics table. I had been eating with the mathematicians and Ifound out that I already knew a fair amount of mathematics; in fact, Iwasn’t learning much. The physics table was, as he said, an excitingplace, but I think he exaggerated on how much I contributed. It wasvery 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 was achemistry 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 I camein one day and said, “If what you are doing is not important, and ifyou don’t think it is going to lead to something important, why are youat Bell Labs working on it?” I wasn’t welcomed after that; I had tofind somebody else to eat with! That was in the spring.
In the fall, Dave McCall stopped me in the halland said, “Hamming, that remark of yours got underneath my skin. Ithought about it all summer, i.e. what were the important problems inmy field. I haven’t changed my research,” he says, “but I think it waswell worthwhile.” And I said, “Thank you Dave,” and went on. I noticeda couple of months later he was made the head of the department. Inoticed the other day he was a Member of the National Academy ofEngineering. I noticed he has succeeded. I have never heard the namesof any of the other fellows at that table mentioned in science andscientific circles. They were unable to ask themselves, “What are theimportant problems in my field?”
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 planting acorns so thatoaks will grow. You can’t always know exactly where to be, but you cankeep active in places where something might happen. And even if youbelieve that great science is a matter of luck, you can stand on amountain top where lightning strikes; you don’t have to hide in thevalley where you’re safe. But the average scientist does routine safework almost all the time and so he (or she) doesn’t produce much. It’sthat simple. If you want to do great work, you clearly must work onimportant problems, and you should have an idea.
Along those lines at some urging from John Tukeyand others, I finally adopted what I called “Great Thoughts Time.” WhenI went to lunch Friday noon, I would only discuss great thoughts afterthat. By great thoughts I mean ones like: “What will be the role ofcomputers in all of AT&T?‘’, “How will computers change science?”For example, I came up with the observation at that time that nine outof ten experiments were done in the lab and one in ten on the computer.I made a remark to the vice presidents one time, that it would bereversed, i.e. nine out of ten experiments would be done on thecomputer and one in ten in the lab. They knew I was a crazymathematician and had no sense of reality. I knew they were wrong andthey’ve been proved wrong while I have been proved right. They builtlaboratories when they didn’t need them. I saw that computers weretransforming science because I spent a lot of time asking “What will bethe impact of computers on science and how can I change it?” I askedmyself, “How is it going to change Bell Labs?” I remarked one time, inthe same address, that more than one-half of the people at Bell Labswill be interacting closely with computing machines before I leave.Well, you all have terminals now. I thought hard about where was myfield going, where were the opportunities, and what were the importantthings to do. Let me go there so there is a chance I can do importantthings.
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 drop allthe other things and get after it. Now I can tell you a horror storythat 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; we didn’tget around to reducing it because we were building some more equipment,but if we had reduced that data we would have found fission.” They hadit in their hands and they didn’t pursue it. They came 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.
I want to talk on another topic. It is based onthe song which I think many of you know, “It ain’t what you do, it’sthe way that you do it.” I’ll start with an example of my own. I wasconned into doing on a digital computer, in the absolute binary days, aproblem which the best analog computers couldn’t do. And I was gettingan answer. When I thought carefully and said to myself, “You know,Hamming, you’re going to have to file a report on this military job;after you spend a lot of money you’re going to have to account for itand every analog installation is going to want the report to see ifthey can’t find flaws in it.” I was doing the required integration by arather crummy method, to say the least, but I was getting the answer.And I realized that in truth the problem was not just to get theanswer; it was to demonstrate for the first time, and beyond question,that I could beat the analog computer on its own ground with a digitalmachine. I reworked the method of solution, created a theory which wasnice and elegant, and changed the way we computed the answer; theresults were no different. The published report had an elegant methodwhich was later known for years as “Hamming’s Method of IntegratingDifferential Equations.” It is somewhat obsolete now, but for a whileit was a very good method. By changing the problem slightly, I didimportant work rather than trivial work.
In the same way, when using the machine up in theattic in the early days, I was solving one problem after another afteranother; a fair number were successful and there were a few failures. Iwent home one Friday after finishing a problem, and curiously enough Iwasn’t happy; I was depressed. I could see life being a long sequenceof one problem after another after another. After quite a while ofthinking I decided, “No, I should be in the mass production of avariable product. I should be concerned with all of nextyear’s problems, not just the one in front of my face.” By changing thequestion I still got the same kind of results or better, but I changedthings and did important work. I attacked the major problem - How do Iconquer machines and do all of next year’s problems when I don’t knowwhat they are going to be? How do I prepare for it? How do I do thisone so I’ll be on top of it? How do I obey Newton’s rule? He said, “IfI have seen further than others, it is because I’ve stood on theshoulders of giants.” These days we stand on each other’s feet!
You should do your job in such a fashion thatothers can build on top of it, so they will indeed say, “Yes, I’vestood on so and so’s shoulders and I saw further.” The essence ofscience is cumulative. By changing a problem slightly you can often dogreat work rather than merely good work. Instead of attacking isolatedproblems, I made the resolution that I would never again solve anisolated problem except as characteristic of a class.
Now if you are much of a mathematician you knowthat the effort to generalize often means that the solution is simple.Often by stopping and saying, “This is the problem he wants but this ischaracteristic of so and so. Yes, I can attack the whole class with afar superior method than the particular one because I was earlierembedded in needless detail.” The business of abstraction frequentlymakes things simple. Furthermore, I filed away the methods and preparedfor the future problems.
To end this part, I’ll remind you, “It is a poorworkman who blames his tools - the good man gets on with the job, givenwhat he’s got, and gets the best answer he can.” And I suggest that byaltering the problem, by looking at the thing differently, you can makea great deal of difference in your final productivity because you caneither do it in such a fashion that people can indeed build on whatyou’ve done, or you can do it in such a fashion that the next personhas to essentially duplicate again what you’ve done. It isn’t just amatter of the job, it’s the way you write the report, the way you writethe paper, the whole attitude. It’s just as easy to do a broad, generaljob as one very special case. And it’s much more satisfying andrewarding!
I have now come down to a topic which is verydistasteful; it is not sufficient to do a job, you have to sell it.‘Selling’ to a scientist is an awkward thing to do. It’s very ugly; youshouldn’t have to do it. The world is supposed to be waiting, and whenyou do something great, they should rush out and welcome it. But thefact is everyone is busy with their own work. You must present it sowell that they will set aside what they are doing, look at what you’vedone, read it, and come back and say, “Yes, that was good.” I suggestthat when you open a journal, as you turn the pages, you ask why youread some articles and not others. You had better write your report sowhen it is published in the Physical Review, or wherever else you wantit, as the readers are turning the pages they won’t just turn yourpages but they will stop and read yours. If they don’t stop and readit, you won’t get credit.
There are three things you have to do in selling.You have to learn to write clearly and well so that people will readit, you must learn to give reasonably formal talks, and you also mustlearn to give informal talks. We had a lot of so-called ‘back roomscientists.’ In a conference, they would keep quiet. Three weeks laterafter a decision was made they filed a report saying why you should doso and so. Well, it was too late. They would not stand up right in themiddle of a hot conference, in the middle of activity, and say, “Weshould do this for these reasons.” You need to master that form ofcommunication as well as 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 to meetings I had already beenstudying why some papers are remembered and most are not. The technicalperson wants to give a highly limited technical talk. Most of the timethe audience wants a broad general talk and wants much more survey andbackground than the speaker is willing to give. As a result, many talksare ineffective. The speaker names a topic and suddenly plunges intothe details he’s solved. Few people in the audience may follow. Youshould paint a general picture to say why it’s important, and thenslowly give a sketch of what was done. Then a larger number of peoplewill say, “Yes, Joe has done that,” or “Mary has done that; I reallysee where it is; yes, Mary really gave a good talk; I understand whatMary has done.” The tendency is to give a highly restricted, safe talk;this is usually ineffective. Furthermore, many talks are filled withfar too much information. So I say this idea of selling is obvious.
Let me summarize. You’ve got to work on importantproblems. I deny that it is all luck, but I admit there is a fairelement of luck. I subscribe to Pasteur’s “Luck favors the preparedmind.” I favor heavily what I did. Friday afternoons for years - greatthoughts only - means that I committed 10% of my time trying tounderstand the bigger problems in the field, i.e. what was and what wasnot important. I found in the early days I had believed ‘this’ and yethad spent all week marching in ‘that’ direction. It was kind offoolish. If I really believe the action is over there, why do I marchin this direction? I either had to change my goal or change what I did.So I changed something I did and I marched in the direction I thoughtwas important. It’s that easy.
Now you might tell me you haven’t got controlover what you have to work on. Well, when you first begin, you may not.But once you’re moderately successful, there are more people asking forresults than you can deliver and you have some power of choice, but notcompletely. I’ll tell you a story about that, and it bears on thesubject of educating your boss. I had a boss named Schelkunoff; he was,and still is, a very good friend of mine. Some military person came tome and demanded some answers by Friday. Well, I had already dedicatedmy computing resources to reducing data on the fly for a group ofscientists; I was knee deep in short, small, important problems. Thismilitary person wanted me to solve his problem by the end of the day onFriday. I said, “No, I’ll give it to you Monday. I can work on it overthe weekend. I’m not going to do it now.” He goes down to my boss,Schelkunoff, and Schelkunoff says, “You must run this for him; he’s gotto have it by Friday.” I tell him, “Why do I?‘’; he says, “You haveto.” I said, “Fine, Sergei, but you’re sitting in your office Fridayafternoon catching the late bus home to watch as this fellow walks outthat door.” I gave the military person the answers late Fridayafternoon. I then went to Schelkunoff’s office and sat down; as the mangoes out I say, “You see Schelkunoff, this fellow has nothing under hisarm; but I gave him the answers.” On Monday morning Schelkunoff calledhim up and said, “Did you come in to work over the weekend?” I couldhear, as it were, a pause as the fellow ran through his mind of whatwas going to happen; but he knew he would have had to sign in, and he’dbetter not say he had when he hadn’t, so he said he hadn’t. Ever afterthat Schelkunoff said, “You set your deadlines; you can change them.”
One lesson was sufficient to educate my boss asto why I didn’t want to do big jobs that displaced exploratory researchand why I was justified in not doing crash jobs which absorb all theresearch computing facilities. I wanted instead to use the facilitiesto compute a large number of small problems. Again, in the early days,I was limited in computing capacity and it was clear, in my area, thata “mathematician had no use for machines.” But I needed more machinecapacity. Every time I had to tell some scientist in some other area,“No I can’t; I haven’t the machine capacity,” he complained. I said “Gotell your Vice President that Hamming needs more computingcapacity.” After a while I could see what was happening up there at thetop; many people said to my Vice President, “Your man needs morecomputing capacity.” I got it!
I also did a second thing. When I loaned whatlittle programming power we had to help in the early days of computing,I said, “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 the topic, “Is the effortto be a great scientist worth it?” To answer this, you must ask people.When you get beyond their modesty, most people will say, “Yes, doingreally first-class work, and knowing it, is as good as wine, women andsong put together,” or if it’s a woman she says, “It is as good aswine, men and song put together.” And if you look at the bosses, theytend to come back or ask for reports, trying to participate in thosemoments of discovery. They’re always in the way. So evidently those whohave done it, want to do it again. But it is a limited survey. I havenever dared to go out and ask those who didn’t do great work how theyfelt about the matter. It’s a biased sample, but I still think it isworth the struggle. I think it is very definitely worth the struggle totry and do first-class work because the truth is, the value is in thestruggle more than it is in the result. The struggle to make somethingof yourself seems to be worthwhile in itself. The success and fame aresort of dividends, in my opinion.
I’ve told you how to do it. It is so easy, so whydo so many people, with all their talents, fail? For example, myopinion, to this day, is that there are in the mathematics departmentat Bell Labs quite a few people far more able and far better endowedthan I, but they didn’t produce as much. Some of them did produce morethan I did; Shannon produced more than I did, and some others produceda lot, but I was highly productive against a lot of other fellows whowere better equipped. Why is it so? What happened to them? Why do somany of the people who have great promise, fail?
Well, one of the reasons is drive and commitment.The people who do great work with less ability but who are committed toit, get more done that those who have great skill and dabble in it, whowork during the day and go home and do other things and come back andwork the next day. They don’t have the deep commitment that isapparently necessary for really first-class work. They turn out lots ofgood work, but we were talking, remember, about first-class work. Thereis a difference. Good people, very talented people, almost always turnout good work. We’re talking about the outstanding work, the type ofwork that gets the Nobel Prize and gets 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 happening again and again; goodscientists will fight the system rather than learn to work with thesystem and take advantage of all the system has to offer. It has a lot,if you learn how to use it. It takes patience, but you can learn how touse the system pretty well, and you can learn how to get around it.After all, if you want a decision ‘No’, you just go to your boss andget a ‘No’ easy. If you want to do something, don’t ask, do it. Presenthim with an accomplished fact. Don’t give him a chance to tell you‘No’. But if you want a ‘No’, it’s easy to get a‘No’.
Another personality defect is ego assertion andI’ll speak in this case of my own experience. I came from Los Alamosand in the early days I was using a machine in New York at 590 MadisonAvenue where we merely rented time. I was still dressing in westernclothes, big slash pockets, a bolo and all those things. I vaguelynoticed that I was not getting as good service as other people. So Iset out to measure. You came in and you waited for your turn; I felt Iwas not getting a fair deal. I said to myself, “Why? No Vice Presidentat IBM said, ‘Give Hamming a bad time’. It is the secretaries at thebottom who are doing this. When a slot appears, they’ll rush to findsomeone to slip in, but they go out and find somebody else. Now, why? Ihaven’t mistreated them.” Answer, I wasn’t dressing the way they feltsomebody in that situation should. It came down to just that - I wasn’tdressing properly. I had to make the decision - was I going to assertmy ego and dress the way I wanted to and have it steadily drain myeffort from my professional life, or was I going to appear to conformbetter? I decided I would make an effort to appear to conform properly.The moment I did, I got much better service. And now, as an oldcolorful character, I get better service than other people.
You should dress according to the expectations ofthe audience spoken to. If I am going to give an address at the MITcomputer center, I dress with a bolo and an old corduroy jacket orsomething else. I know enough not to let my clothes, my appearance, mymanners get in the way of what I care about. An enormous number ofscientists feel they must assert their ego and do their thing theirway. They have got to be able to do this, that, or the other thing, andthey pay a steady price.
John Tukey almost always dressed very casually.He would go into an important office and it would take a long timebefore the other fellow realized that this is a first-class man and hehad better listen. For a long time John has had to overcome this kindof hostility. It’s wasted effort! I didn’t say you should conform; Isaid “The appearance of conforming gets you a long way.” Ifyou chose to assert your ego in any number of ways, “I am going to doit my way,” you pay a small steady price throughout the whole of yourprofessional career. And this, over a whole lifetime, adds up to anenormous amount of needless trouble.
By taking the trouble to tell jokes to thesecretaries and being a little friendly, I got superb secretarial help.For instance, one time for some idiot reason all the reproducingservices at Murray Hill were tied up. Don’t ask me how, but they were.I wanted something done. My secretary called up somebody at Holmdel,hopped the company car, made the hour-long trip down and got itreproduced, and then came back. It was a payoff for the times I hadmade an effort to cheer her up, tell her jokes and be friendly; it wasthat little extra work that later paid off for me. By realizing youhave to use the system and studying how to get the system to do yourwork, you learn how to adapt the system to your desires. Or you canfight it steadily, as a small undeclared war, for the whole of yourlife.
And I think John Tukey paid a terrible priceneedlessly. He was a genius anyhow, but I think it would have been farbetter, and far simpler, had he been willing to conform a little bitinstead of ego asserting. He is going to dress the way he wants all ofthe time. It applies not only to dress but to a thousand other things;people will continue to fight the system. Not that you shouldn’toccasionally!
When they moved the library from the middle ofMurray Hill to the far end, a friend of mine put in a request for abicycle. Well, the organization was not dumb. They waited awhile andsent back a map of the grounds saying, “Will you please indicate onthis map what paths you are going to take so we can get an insurancepolicy covering you.” A few more weeks went by. They then asked, “Whereare you going to store the bicycle and how will it be locked so we cando so and so.” He finally realized that of course he was going to bered-taped to death so he gave in. He rose to be the President of BellLaboratories.
Barney Oliver was a good man. He wrote a letterone time to the IEEE. At that time the official shelf space at BellLabs was so much and the height of the IEEE Proceedings at that timewas larger; and since you couldn’t change the size of the officialshelf space he wrote this letter to the IEEE Publication person saying,“Since so many IEEE members were at Bell Labs and since the officialspace was so high the journal size should be changed.” He sent it forhis boss’s signature. Back came a carbon with his signature, but hestill doesn’t know whether the original was sent or not. I am notsaying you shouldn’t make gestures of reform. I am saying that my studyof able people is that they don’t get themselves committed to that kind of warfare. They play it a little bit and drop it and get on with their work.
Many a second-rate fellow gets caught up in somelittle twitting of the system, and carries it through to warfare. Heexpends his energy in a foolish project. Now you are going to tell methat somebody has to change the system. I agree; somebody’s has to.Which do you want to be? The person who changes the system or theperson who does first-class science? Which person is it that you wantto be? Be clear, when you fight the system and struggle with it, whatyou are doing, how far to go out of amusement, and how much to wasteyour effort fighting the system. My advice is to let somebody else doit and you get on with becoming a first-class scientist. Very few ofyou have the ability to both reform the system and become a first-class scientist.
On the other hand, we can’t always give in. Thereare times when a certain amount of rebellion is sensible. I haveobserved almost all scientists enjoy a certain amount of twitting thesystem for the sheer love of it. What it comes down to basically isthat you cannot be original in one area without having originality inothers. Originality is being different. You can’t be an originalscientist without having some other original characteristics. But manya scientist has let his quirks in other places make him pay a farhigher price than is necessary for the ego satisfaction he or she gets.I’m not against all ego assertion; I’m against 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 you should look for is the positiveside of things instead of the negative. I have already given youseveral examples, and there are many, many more; how, given thesituation, by changing the way I looked at it, I converted what wasapparently a defect to an asset. I’ll give you another example. I am anegotistical person; there is no doubt about it. I knew that most peoplewho took a sabbatical to write a book, didn’t finish it on time. Sobefore I left, I told all my friends that when I come back, that bookwas going to be done! Yes, I would have it done - I’d have been ashamedto come back without it! I used my ego to make myself behave the way Iwanted to. I bragged about something so I’d have to perform. I foundout many times, like a cornered rat in a real trap, I was surprisinglycapable. I have found that it paid to say, “Oh yes, I’ll get the answerfor you Tuesday,” not having any idea how to do it. By Sunday night Iwas really hard thinking on how I was going to deliver by Tuesday. Ioften put my pride on the line and sometimes I failed, but as I said,like a cornered rat I’m surprised how often I did a good job. I thinkyou need to learn to use yourself. I think you need to know how toconvert a situation from one view to another which would increase thechance of success.
Now self-delusion in humans is very, very common.There are enumerable ways of you changing a thing and kidding yourselfand making it look some other way. When you ask, “Why didn’t you dosuch and such,” the person has a thousand alibis. If you look at thehistory of science, usually these days there are 10 people right thereready, and we pay off for the person who is there first. The other ninefellows say, “Well, I had the idea but I didn’t do it and so on and soon.” There are so many alibis. Why weren’t you first? Why didn’t you doit right? Don’t try an alibi. Don’t try and kid yourself. You can tellother people all the alibis you want. I don’t mind. But to yourself tryto be honest.
If you really want to be a first-class scientistyou need to know yourself, your weaknesses, your strengths, and yourbad faults, like my egotism. How can you convert a fault to an asset?How can you convert a situation where you haven’t got enough manpowerto move 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.
In summary, I claim that some of the reasons whyso many people who have greatness within their grasp don’t succeed are:they don’t work on important problems, they don’t become emotionallyinvolved, they don’t try and change what is difficult to some othersituation which is easily done but is still important, and they keepgiving themselves alibis why they don’t. They keep saying that it is amatter of luck. I’ve told you how easy it is; furthermore I’ve told youhow to reform. Therefore, go forth and become great scientists!
(End of the formal part of the talk.)
DISCUSSION - QUESTIONS AND ANSWERS
A. G. Chynoweth: Well that was 50 minutes of concentrated wisdom and observationsaccumulated over a fantastic career; I lost track of all theobservations 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 was awonderful 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: Firstlet me respond to Alan Chynoweth about computing. I had computing inresearch and for 10 years I kept telling my management, “Get that!&@#% machine out of research. We are being forced to run problemsall the time. We can’t do research because were too busy operating andrunning the computing machines.” Finally the message got through. Theywere going to move computing out of research to someplace else. I waspersona non grata to say the least and I was surprised that peopledidn’t kick my shins because everybody was having their toy taken awayfrom them. I went in to Ed David’s office and said, “Look Ed, you’vegot to give your researchers a machine. If you give them a great bigmachine, we’ll be back in the same trouble we were before, so busykeeping it going we can’t think. Give them the smallest machine you canbecause they are very able people. They will learn how to do things ona small machine instead of mass computing.” As far as I’m concerned,that’s how UNIX arose. We gave them a moderately small machine and theydecided to make it do great things. They had to come up with a systemto do it on. It is called UNIX!
A. G. Chynoweth: I just have to pick up on that one. In our present environment, Dick,while we wrestle with some of the red tape attributed to, or requiredby, the regulators, there is one quote that one exasperated AVP came upwith and I’ve used it over and over again. He growled that, “UNIX wasnever 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: Theremarks about having courage, no one could argue with; but those of uswho have gray hairs or who are well established don’t have to worry toomuch. But what I sense among the young people these days is a realconcern over the risk taking in a highly competitive environment. Doyou have any words of wisdom on this?
Hamming: I’llquote Ed David more. Ed David was concerned about the general loss ofnerve 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: Oncethat was a very popular thing, but it seems not to have paid off. Formyself I find it desirable to talk to other people; but a session ofbrainstorming is seldom worthwhile. I do go in to strictly talk tosomebody and say, “Look, I think there has to be something here. Here’swhat I think I see …” and then begin talking back and forth. But youwant to pick capable people. To use another analogy, you know the ideacalled the ‘critical mass.’ If you have enough stuff you have criticalmass. There is also the idea I used to call ‘sound absorbers’. When youget too many sound absorbers, you give out an idea and they merely say,“Yes, yes, yes.” What you want to do is get that critical mass inaction; “Yes, that reminds me of so and so,” or, “Have you thoughtabout that or this?” When you talk to other people, you want to get ridof those sound absorbers who are nice people but merely say, “Oh yes,”and to find those who will stimulate you right back.
For example, you couldn’t talk to John Piercewithout being stimulated very quickly. There were a group of otherpeople I used to talk with. For example there was Ed Gilbert; I used togo down to his office regularly and ask him questions and listen andcome back stimulated. I picked my people carefully with whom I did orwhom I didn’t brainstorm because the sound absorbers are a curse. Theyare just nice guys; they fill the whole space and they contributenothing except they absorb ideas and the new ideas just die awayinstead of echoing on. Yes, I find it necessary to talk to people. Ithink people with closed doors fail to do this so they fail to gettheir ideas sharpened, such as “Did you ever notice something overhere?” I never knew anything about it - I can go over and look.Somebody points the way. On my visit here, I have already found severalbooks that I must read when I get home. I talk to people and askquestions when I think they can answer me and give me clues that I donot 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: Ibelieved, in my early days, that you should spend at least as much timein the polish and presentation as you did in the original research. Nowat least 50% of the time must go for the presentation. It’s a big, bignumber.
Question: How much effort should go into library work?
Hamming: Itdepends upon the field. I will say this about it. There was a fellow atBell 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: Bydoing 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; you knowperfectly well I did only a small part of the work but you also did alot.” He said, “Yes, Hamming, but you contributed a lot of smallthings; you’re entitled to some credit.” So he called it the hammingwindow. Now, let me go on. I had twitted John frequently about truegreatness. 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: Inthe 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: Youmentioned the problem of the Nobel Prize and the subsequent notorietyof what was done to some of the careers. Isn’t that kind of a much morebroad problem of fame? What can one do?
Hamming: Somethings you could do are the following. Somewhere around every sevenyears make a significant, if not complete, shift in your field. Thus, Ishifted from numerical analysis, to hardware, to software, and so on,periodically, because you tend to use up your ideas. When you go to anew field, you have to start over as a baby. You are no longer the bigmukity muk and you can start back there and you can start plantingthose acorns which will become the giant oaks. Shannon, I believe,ruined himself. In fact when he left Bell Labs, I said, “That’s the endof Shannon’s scientific career.” I received a lot of flak from myfriends who said that Shannon was just as smart as ever. I said, “Yes,he’ll be just as smart, but that’s the end of his scientific career,”and I truly believe it was.
You have to change. You get tired after a while;you use up your originality in one field. You need to get somethingnearby. I’m not saying that you shift from music to theoretical physicsto English literature; I mean within your field you should shift areasso that you don’t go stale. You couldn’t get away with forcing a changeevery seven years, but if you could, I would require a condition fordoing research, being that you will change your field ofresearch every seven years with a reasonable definition of what itmeans, or at the end of 10 years, management has the right to compelyou to change. I would insist on a change because I’m serious. Whathappens to the old fellows is that they get a technique going; theykeep on using it. They were marching in that direction which was rightthen, but the world changes. There’s the new direction; but the oldfellows are still marching in their former direction.
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 ittakes effort and energy. It takes courage to say, “Yes, I will give upmy great reputation.” For example, when error correcting codes werewell launched, having these theories, I said, “Hamming, you are goingto quit reading papers in the field; you are going to ignore itcompletely; you are going to try and do something else other than coaston that.” I deliberately refused to go on in that field. I wouldn’teven read papers to try to force myself to have a chance to dosomething else. I managed myself, which is what I’m preaching in thiswhole talk. Knowing many of my own faults, I manage myself. I have alot of faults, so I’ve got a lot of problems, i.e. a lot ofpossibilities of management.
Question: Would you compare research and management?
Hamming: Ifyou want to be a great researcher, you won’t make it being president ofthe company. If you want to be president of the company, that’s anotherthing. I’m not against being president of the company. I just don’twant to be. I think Ian Ross does a good job as President of Bell Labs.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 had to make it happen; I had to be department head.” When your vision of what you want to do iswhat you can do single-handedly, then you should pursue it. The dayyour vision, what you think needs to be done, is bigger than what youcan do single-handedly, then you have to move toward management. Andthe bigger the vision is, the farther in management you have to go. Ifyou have a vision of what the whole laboratory should be, or the wholeBell System, you have to get there to make it happen. You can’t make ithappen from the bottom very easily. It depends upon what goals and whatdesires you have. And as they change in life, you have to be preparedto change. I chose to avoid management because I preferred to do what Icould do single-handedly. But that’s the choice that I made, and it isbiased. Each person is entitled to their choice. Keep an open mind. Butwhen you do choose a path, for heaven’s sake be aware of what you havedone and the choice you have made. Don’t try to do both sides.
Question: Howimportant is one’s own expectation or how important is it to be in agroup or surrounded by people who expect great work from you?
Hamming: AtBell 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 youseemed also to gloss over the circumstances that got you to Los Alamos,that got you to Chicago, that got you to Bell Laboratories.
Hamming: Therewas some luck. On the other hand I don’t know the alternate branches.Until you can say that the other branches would not have been equallyor more successful, I can’t say. Is it luck the particular thing youdo? For example, when I met Feynman at Los Alamos, I knew he was goingto get a Nobel Prize. I didn’t know what for. But I knew darn well hewas going to do great work. No matter what directions came up in thefuture, this man would do great work. And sure enough, he did do greatwork. It isn’t that you only do a little great work at thiscircumstance and that was luck, there are many opportunities sooner orlater. There are a whole pail full of opportunities, of which, ifyou’re in this situation, you seize one and you’re great over thereinstead of over here. There is an element of luck, yes and no. Luckfavors a prepared mind; luck favors a prepared person. It is notguaranteed; I don’t guarantee success as being absolutely certain. I’dsay luck changes the odds, but there is some definite control on thepart of the individual.
Go forth, then, and do great work!
(End of the General Research Colloquium Talk.)
Transcription of the Bell Communications Research Colloquium Seminar
7 March 1986
J. F. Kaiser
Bell Communications Research
445 South Street
Morristown, NJ 07962-1910
jfk@bellcore.com