You and Your Research

Why Do First-Rate Work?

👦🏻 Author: Richard Hamming

🥷 Compiled by: NCon

Editor's Note from Crossing (Koji)

During the National Day holiday, we're digging up a few classic articles to share.

This time we've selected a 1986 lecture by American mathematician and computer scientist Richard Hamming.

He observed many outstanding scientists, spoke frankly about his own envy, confusion, and choices, then brought a question before us: Is what I'm spending my time on worth doing?

During the holiday, perhaps you can temporarily set aside progress and think about this question. While reading, you need not accept all of his trade-offs; we can bring our own lives and compare them with his experience.

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Why Do First-Rate Work?

The title of my talk today is "You and Your Research." I'm going to talk about how you personally do research, not how to manage research. I could talk about the latter too, but today it's about you.

I'm not talking about run-of-the-mill research, but great research. To illustrate what I mean by great research, I sometimes use the phrase "Nobel-Prize-quality work." It doesn't necessarily have to win a Nobel Prize, but it's the kind of work we consider significant.

Things like relativity, Shannon's information theory, and many outstanding theories — that's the kind of work I mean.

Why did I study this question?

At Los Alamos, I was brought in to operate computing equipment that others had already started up, so those scientists and physicists could get back to their own work. I found myself just a hired hand. Physically, I was no different from them, but they were different from me.

Frankly, I envied them. I wanted to know why they were so different from me.

I worked closely with Feynman, Fermi, Teller, Oppenheimer, and Hans Bethe — he was my boss. I met quite a few very capable people. I became deeply interested in a question: What distinguishes those who actually achieve something from those who merely had the potential?

Later I came to Bell Labs and entered a very productive department. The department head at the time was Bode, Shannon was there too, and others.

I kept asking: "Why?" "What's the difference?"

After that, I sought answers by reading biographies and autobiographies, by asking people questions like: "How did you do this piece of work?" I always wanted to understand these differences. That's what today's talk is about.

Why does this matter?

I think it matters because, as far as I know, you each have only one life. Even if you believe in reincarnation, one lifetime doesn't help the next one!

Since you only have one life, why not do something meaningful? As for what counts as meaningful, you can define that yourself. I'm not going to define it for you — you know what I mean.

I'll mainly talk about science because that's the field I've studied. But as far as I know, and as others have told me, much of what I'll say applies equally to other fields. In most fields, the characteristics of outstanding work are very similar, though today I'll limit my scope to science.

To get each of you to really listen, I have to speak in the first person. I have to get you to temporarily set aside modesty and say to yourself: "Yes, I want to do first-rate work."

Our society doesn't much admire those who set out from the start to do truly excellent work. You apparently shouldn't think this way; you should wait for good fortune to fall from the sky, and then happen to do something great.

This is rather foolish. What I want to say is: Why not actively go and do something meaningful?

You don't have to tell anyone, but shouldn't you say to yourself: "Yes, I want to do something meaningful."

To push this further, I too must set aside modesty and speak in the first person about what I've seen, done, and heard.

I'll mention some people, some of whom you know too. I trust that after leaving here, you won't quote certain things I say today.

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Chance Favors the Prepared Mind

I'll start with the psychological rather than the logical.

I find that the most common objection is: great scientific achievements depend on luck, it's all a matter of luck.

Well, think about Einstein. Look at how many different things he did well. All luck? Does this "good fortune" repeat itself rather too often?

Look at Shannon too. He didn't just do information theory. Years earlier, he had already done some excellent work, some of which remains unpublished due to cryptography secrecy requirements even today. He produced many good results.

You'll see again and again that an outstanding person usually accomplishes more than one thing. Occasionally someone does only one great thing in their life, which we'll get to later, but many people's achievements recur.

I don't think luck explains everything. Pasteur said: "Chance favors the prepared mind." This expresses my view exactly.

There is indeed an element of luck, but it can't all be reduced to luck. The prepared mind will sooner or later discover something important and get it done.

So yes, there's luck. Which particular thing you accomplish may depend on luck; but that you eventually accomplish something is not just luck.

For example, when I first came to Bell Labs, there was a period when I shared an office with Shannon. He was working on information theory while I was working on coding theory.

That we both did this work in the same place, at the same time, is really worth pondering — the ideas were simply in the air then. You could say: "Yes, this was luck."

But you could also ask: "There were so many people at Bell Labs then, why was it those two who did it?"

Yes, partly luck, partly prepared minds. The latter is the other thing I want to talk about.

So though I'll mention luck a few more times later, I want to first dismiss the view that luck is the sole determinant of whether you can do great work. I think you have some control over this, just not complete control.

Finally, another quote from Newton: "If others would think as hard as I did, they would get similar results."

You'll find a characteristic that many people have, great scientists included: they often had independent ideas when young, and dared to follow them through.

For instance, at about age twelve or fourteen, Einstein asked himself: "If I were to chase a light wave at the speed of light, what would it look like?"

He knew that electromagnetic theory doesn't allow stationary local maxima. But if he moved at the speed of light along with the light wave, he would see a local maximum.

At twelve, fourteen, or thereabouts, he already saw the contradiction: something was wrong, light speed had something special about it. Was it pure luck that he later created special relativity?

He started thinking about these fragments very early, laying some groundwork for his later work. Of course, this was necessary but not sufficient. The factors I'll discuss all have both lucky and non-lucky components.

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Beyond Brains, You Need Courage

What about being exceptionally smart? That sounds good, of course. Most of you here probably have more than enough intelligence to do first-rate work.

But great work requires more than brains.

There are many ways to measure intelligence. In mathematics, theoretical physics, and astrophysics, intelligence often manifests largely as symbol-manipulation ability. So these people tend to score very high on typical IQ tests. But in other fields, intelligence may appear as something else.

For example, Bill Pfann, who invented zone melting, came into my office one day. He had a vague idea of what he wanted to do, and some equations in hand.

I could clearly see that this man didn't know much mathematics, and wasn't very articulate. But his problem seemed interesting, so I took it home and did some work on it.

Eventually, I taught him how to use computers so he could calculate answers himself. I gave him the power of computation.

He kept going, receiving almost no recognition from his own department, but in the end, he won all the prizes in that field.

Once he really broke through, his shyness, awkwardness, and inarticulateness gradually fell away, and he became productive in many other ways too. At least, his ability to express himself improved greatly.

I can give another similar example. I hope he's not in the audience today — this man was Clogston.

I met him while working on a problem with John Pierce's group. I thought he had no ability.

I asked friends who had gone to school with him: "Was he like this in graduate school?" They said: "Yes."

If it had been me, I probably would have fired him long ago. But J. R. Pierce was wise and kept him on. Later, Clogston invented the Clogston cable.

After that, good ideas kept pouring out of him. One success gave him confidence and courage.

One characteristic of successful scientists is courage. Once you summon the courage to believe you can solve important problems, you may well do so. Conversely, if you believe you can't, you almost certainly won't.

One of Shannon's most outstanding qualities was courage. Just think of that important theorem of his.

He wanted to create a coding method but didn't know how, so he first constructed a random code. Then he got stuck. Then he asked what seemed an impossibly answerable question: "How will the average random code perform?"

He then proved that on average, these codes could be arbitrarily close to ideal, and therefore at least one good code must necessarily exist.

Without infinite courage, who would dare think this way?

This is the mark of great scientists: they have courage. Even in unimaginable circumstances, they press on; they think, and keep thinking.

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After Fame, Don't Stop Planting Seeds

Age is another factor, one that physicists especially worry about. They always say: you have to do it while you're young, or you'll never do it.

Einstein achieved early, and those who worked on quantum mechanics were unbearably young when they did their best work.

Most mathematicians, theoretical physicists, and astrophysicists do what we consider their best work when young. This isn't to say they have no good results later in life, but what we value most is often their early work.

On the other hand, in music, politics, and literature, what we consider the finest works or achievements often appear in later years.

I don't know where on this spectrum your respective fields lie, but age does have an effect.

However, let me say why age seems to have this effect.

First, once you produce some good results, you find yourself pulled onto various committees and can no longer continue doing research.

You may also encounter what I saw in Brattain. The day the Nobel Prize was announced, we all gathered in Arnold Auditorium, and the three laureates each went up to speak.

The third to speak was Brattain. He said, almost with tears in his eyes, "I know about this 'Nobel Prize effect.' I will not let it affect me. I am still the same Walter Brattain."

I thought to myself: "That's good."

But a few weeks later, I saw that he had been affected. Now he would only work on big problems.

Once you become famous, it's very hard to keep working on small problems. Shannon was held back by this. After creating information theory, what could he possibly do for an encore?

Great scientists often make this mistake. They stop planting the little acorns that can grow into mighty oaks, and instead try to jump straight to big results. But things don't usually work that way.

So premature recognition seems to destroy a person's ability to keep creating — that's one reason.

Let me say one more thing, a favorite line of mine for many years: In my opinion, the Institute for Advanced Study at Princeton has destroyed more great scientists than any institution has ever produced — you need only compare their work before they went there with their work after.

It's not that they weren't good after they went there. It's that they were extremely good before, and merely good after.

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Turning Disadvantages into Advantages

This brings up the question of working conditions, though it's perhaps a bit out of sequence to discuss it now.

Most people think the best working conditions are not actually the best. This is obvious, because people are often most productive when conditions are poor.

The most glorious period of the Cavendish Laboratory was when it was essentially a collection of shabby sheds, yet they produced some of the finest physics research ever done.

Let me tell you a story of my own.

Early on, I discovered that Bell Labs would not follow the conventional practice of the time and assign me a large team of programmers to code computers in pure binary. Clearly, they weren't going to do this, though everyone else was.

I could easily have gone to the West Coast and found work at an aircraft company. But the people who excited me were at Bell Labs, not at some aircraft company out there.

For a long time I wondered: "Should I leave or not?" I also puzzled over how I might have the best of both worlds.

Finally, I said to myself: "Hamming, you think machines can do almost anything. Why can't they write their own programs?"

What initially seemed like a disadvantage forced me onto the path of automatic programming very early.

Some conditions that seem unfavorable, viewed from another angle, often become your most valuable advantages.

But when you first face a problem and think, "My God, I'll never get enough programmers to do great programming," you usually don't see this.

There are many similar stories. Grace Hopper had such an experience.

I think if you look carefully, you'll find that great scientists often simply turn a problem slightly and transform a defect into an advantage.

For instance, many scientists find they cannot solve a certain problem, and eventually begin to study: why can't they solve it?

Then they turn it around and say: "Of course, that's what the problem is!" And they obtain important results.

So ideal working conditions are peculiar. The conditions you want are not necessarily the conditions that suit you best.

The Compound Interest of Knowledge and Productivity

Next, let me talk about drive.

You'll find that most great scientists have tremendous drive. I worked with John Tukey at Bell Labs for ten years, and he was such a person.

About three or four years after I arrived, I suddenly discovered one day that Tukey was actually slightly younger than me. He was a genius, and I clearly was not.

I stormed into Bode's office and asked: "How can someone about my age know as much as John Tukey does?"

He leaned back in his chair, put his hands behind his head, smiled slightly, and said: "Hamming, if you had worked as hard as he has for as many years, you would be astonished at how much you could know."

I could only slink out of the office!

Bode's point was: Knowledge and productivity are like compound interest.

Given two people with approximately equal ability, if one works ten percent harder than the other, the final output may be more than twice as great.

The more you know, the more you can learn; the more you learn, the more you can do; the more you do, the more opportunities you have — it's very much like compound interest. I don't want to give a specific rate, but it's high.

Two people of identical ability, if one can think just one hour more each day, day after day, the accumulated results over a lifetime will be astonishing.

I took Bode's words to heart. In the years that followed, I spent more time trying to work a little harder. I found that I could indeed get more done.

I'm somewhat reluctant to say this in front of my wife, but sometimes I did neglect her somewhat, because I needed to study. To accomplish what you want, you must give up other things. There's no doubt about that.

Speaking of drive, Edison said: "Genius is one percent inspiration and ninety-nine percent perspiration."

He may have exaggerated, but his point was: solid, continuous work will take you far beyond what you expect.

Sustained effort, doing a little more, and directing your energy to the right place — these are the things that matter.

Here's the problem: drive applied in the wrong direction doesn't get you anywhere.

I often wondered why so many good friends at Bell Labs, working as hard as I did or even harder, didn't produce corresponding results.

Working hard in the wrong direction is a very serious problem. Effort alone is not enough; you must apply effort in the right places.

Between Belief and Doubt

I also want to mention another trait: the ability to tolerate ambiguity and uncertainty. It took me a while to discover its importance.

Most people like to decide whether something is true or false. Great scientists tolerate uncertainty very well.

They believe in their theories enough to keep pushing forward; yet they remain sufficiently skeptical to spot errors and defects, and thereby create new theories to replace them.

Believe too deeply, and you won't see the holes; doubt too much, and you can't get started.

This requires a delicate balance. Most great scientists know both why their theories work and where the subtle discrepancies lie, and they don't forget these problems.

Darwin wrote in his autobiography that he found he had to write down every piece of evidence that seemed to contradict his beliefs, or else it would disappear from his mind.

When you find obvious defects, you must remain sensitive, record them, and keep watching: how might these be explained, or how might the theory be modified to accommodate them?

Major contributions often arise here. Great contributions rarely come from merely computing a result to one more decimal place.

Ultimately, you need genuine emotional commitment. Most great scientists are completely absorbed in their problems; those who cannot commit in this way rarely do outstanding, first-class work.

Yet emotional commitment alone is still not enough. It is clearly a necessary condition, and I think I can explain why.

Researchers of creativity almost always end up saying: "Creativity comes from the subconscious." Somehow, the answer is just there. It simply appears.

We know very little about the subconscious, but one thing everyone knows: dreams also come from the subconscious. And you know, dreams largely reprocess the day's experiences.

If you immerse yourself in a subject day after day, with complete commitment, your subconscious has nothing else to do but work on that problem.

Then one morning, or some afternoon, the answer appears.

Those who are not genuinely committed to their current problem — their subconscious goes off to work on other things, and they don't produce major results.

So one way to manage yourself: when you face a truly important problem, don't let other things occupy the center of your attention. Keep your thoughts circling around this problem.

Let your subconscious go "hungry," with nothing else to chew on but this problem. Then you can sleep soundly, and wake in the morning with the answer for free.

Spend Your Time on Important Problems

Earlier, Alan Chynoweth mentioned that I used to eat with the physicists.

At first, I ate with the mathematicians. But I found that I already knew enough mathematics that I wasn't really learning much new.

As he said, the physicists' table was exciting, though I think he exaggerated my contribution.

Listening to Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay, and others was fascinating, and I learned a great deal.

Unfortunately, later some won Nobel Prizes, some were promoted, and what remained was just the residue. None of the remaining people were interesting. Since that was so, there was no point in eating with them anymore!

On the other side of the dining room was a table of chemists. I had collaborated with Dave McCall among them, and besides, he was courting our secretary.

I went over and asked: "Mind if I join you?" They could hardly say no, so I began eating with them.

My first question was: "What are the important problems in your field?"

About a week later, I asked: "What important problems are you working on?"

After some more time, one day I went over and said: "If what you're doing is not important, and you don't think it will lead to anything important, why are you doing it at Bell Labs?"

After that, I was no longer welcome and had to find others to eat with! That happened in the spring.

By fall, Dave McCall stopped me in the corridor and said: "Hamming, that remark of yours has been sticking in my craw. I've thought about it all summer: what are the important problems in my field?"

He said: "My research hasn't changed, but I think the exercise was worthwhile."

I said: "Thank you, Dave," and walked on.

A few months later, I noticed he had become head of the department. The other day, I found he is now a member of the National Academy of Engineering. I watched his success.

The names of the others at that table — I have never heard them mentioned again in the scientific community. They could not ask themselves that question: "What are the important problems in my field?"

If you don't work on important problems, it's hard to do important work. This is obvious.

Great scientists seriously think through a set of important problems in their field, and always watch for: where should one begin to attack them?

But I must caution you, the phrase "important problem" must be understood carefully.

During my time at Bell Labs, in a sense, there were three extremely important problems in physics that we never worked on. By extremely important, I mean that solving any of them would certainly win a Nobel Prize, and any amount of money you can imagine.

We did not work on: first, time travel; second, teleportation; third, antigravity.

They do not count as important problems in the sense I mean, because we had no feasible approach to them.

What makes a problem important is not the consequences of solving it, but that you have a reasonable line of attack.

When I say most scientists are not working on important problems, this is what I mean.

In my observation, the average scientist spends almost all their time on problems they themselves do not consider important, and which they do not believe will lead to important problems.

Earlier I spoke of planting acorns so that oaks may grow.

You cannot always know precisely where you should stand, but you can keep yourself active in places where important things are likely to happen.

Even if you believe that great scientific results depend on luck, you can stand on the mountaintop where lightning is likely to strike, rather than hiding in the safe valley.

Yet ordinary scientists spend nearly all their time doing routine, safe work, and therefore don't accomplish very much. It's that simple.

If you want to do great work, you obviously have to work on important problems, and have some notion of how to attack them.

Make time for great thoughts

Along these lines, at the urging of John Tukey and others, I eventually set aside what I called "Great Thoughts Time."

Every Friday after lunch, from then on, I would only discuss great problems.

Great problems like: "What role will computing play in all of AT&T?" "How will computing change science?"

For example, I noticed at the time that nine out of ten experiments were done in the lab, and one on the computer.

I told several vice presidents that the ratio would eventually flip: nine out of ten experiments would be done on the computer, and one in the lab.

They decided I was a crazy, impractical mathematician. I knew they were wrong, and later events proved they were wrong and I was right. They built labs they didn't need.

I could see that computing was changing science because I spent a lot of time asking: "What impact will computing have on science? How can I help shape that change?"

I also asked myself: "How will it change Bell Labs?"

In the same talk, I also said: Before I leave, more than half the people at Bell Labs will be working closely with computers. Now, you all have terminals.

I thought hard about where my field was going, where the opportunities were, what was worth doing. I wanted to be in those places, so I'd have a chance to do important work.

Most great scientists know many important problems. They typically have ten to twenty problems in mind, always looking for an opening.

Whenever a new idea comes up, you'll hear them say: "That relates to such-and-such problem." Then they drop everything else and pursue it full force.

I can tell you a frightening story someone told me, though I can't guarantee it's true.

Once I was chatting with a friend from Los Alamos at the airport. I said how fortunate it was that nuclear fission experiments had succeeded in Europe just then, because it spurred the US to work on the atomic bomb.

He said: "That's not how it was. We had already collected a batch of data at UC Berkeley, but we were so busy building more equipment that we never found time to organize and analyze it. If we had analyzed that data, we would have discovered nuclear fission."

The discovery was already in their hands, and they didn't follow through. As a result, they came in second!

Great scientists, the moment they see an opportunity, grab it and run with it. They drop everything else, clear other tasks, and throw themselves fully into an idea—because they've already thought through the problems.

Their minds are prepared; when they see the opportunity, they immediately pursue it.

Of course, it often doesn't work out. But you don't need to hit very many times to do great scientific work.

In that sense, things are a bit simple. One of the main tricks is simply to live longer!

Keep your door open

There's another characteristic I also noticed only after quite some time.

I've observed people who work with their office door open, and those who work with it closed.

If you work with your door closed, today and tomorrow you will indeed get more work done, more efficiently than most people.

But ten years later, somehow, you can't quite tell which problems are worth working on. The effort you put in keeps drifting away from what truly matters.

People who work with their door open get interrupted constantly, but they also pick up clues about what's happening in the outside world, what might be important.

Of course, I can't prove the causation here. You might say: "A closed door merely symbolizes a closed mind." I don't know.

But I can say there's a fairly strong correlation between working with your door open and eventually doing important work. People who work with their door closed, though often working harder, always seem to be working on things slightly off target.

Not by much, but enough to miss becoming famous.

From solving one problem to solving a class of problems

Now let me change topics. I want to introduce it with a song many of you have probably heard: "It ain't what you do, it's the way that you do it."

Let me start with my own example. Back in the days of pure binary programming, I was talked into taking on a task: using a digital computer to solve a problem that even the best analog computer couldn't solve.

I had already computed the answer. But thinking it over, I said to myself: "Hamming, this is a military project; you ultimately have to submit a report. With all that money spent, there has to be something to show for it. Every institution with analog computing equipment will want to get this report and see if they can find fault with it."

At the time, my method of numerical integration was, to put it politely, rather crude, but it did get the answer.

Then I realized that the real problem wasn't just getting the answer—it was proving for the first time, beyond any doubt, that a digital computer could beat an analog computer on its own home turf.

So I redesigned the solution, built up a beautiful and elegant theory, and changed the way the answer was computed. The final answer didn't change.

But the published report contained an elegant method. For many years afterward, people called it "Hamming's method of integrating differential equations."

It's somewhat outdated now, but there was a time when it was a very good method.

By slightly changing the problem, I turned a routine job into an important one.

Something similar happened another time.

In my early days using the machine up in the attic, I kept solving one problem after another. Quite a few got solved; some failed.

One Friday, after finishing a problem, I went home. Strangely, I wasn't happy—I was depressed. I could already see my whole life stretching out as an endless sequence of solving one problem after another.

After thinking for a long time, I made a decision: "No, what I should do is turn out results in batches. I should care about all the problems that will come up next year, not just this one right in front of me."

By changing how I framed the problem, I still got results that were just as good, or even better, but the way of working changed, and I therefore did important work.

I started attacking the bigger problem: I don't yet know what problems I'll face next year; how can I master these machines to solve them all? What should I prepare? How should I solve this current problem so that I gain the initiative?

How can I follow what Newton said?

He said: "If I have seen further, it is by standing on the shoulders of giants."

These days, we mostly step on each other's feet!

You should do your work in a way that others can build on top of it.

So they can honestly say: "Yes, I stood on so-and-so's shoulders, and therefore saw further."

The essence of science is accumulation. By slightly changing the problem, you can often do great work rather than merely good work.

So I made up my mind: never again solve an isolated problem unless as representative of a whole class of problems.

If you know enough mathematics, you know that trying to generalize a problem often makes the solution simpler.

You stop and think: "This is the problem he wanted solved, but it actually represents a class of problems. Yes, I can solve this whole class of problems in a way far better than the original. Before, I was just mired in unnecessary details."

Abstraction often makes things simpler.

Furthermore, I saved these methods to be ready for problems that would arise later.

Before this section ends, I want to remind you of something: "A poor workman blames his tools; a good workman uses whatever he has at hand, keeps working, and does the best he can."

I want to say that changing how you frame a problem, looking at it from a different angle, enormously affects what you ultimately produce.

You can work in a way that lets people truly build on your results; or you can work in another way, so that later people basically have to redo what you've already done.

This depends not only on the work itself, but on how you write your reports, how you write your papers, and your overall attitude.

Doing work that is broad and general is no harder than solving an extremely special case, yet brings vastly greater satisfaction and reward!

Let people see your work

Now I want to talk about a very uncomfortable topic: doing good work isn't enough—you also have to sell it.

For scientists, "selling" is embarrassing. It's ugly; you shouldn't have to do it.

The world should just be there waiting; when you do something great, everyone should come flocking to welcome it.

But the reality is, everyone is busy with their own work.

You have to present your results well enough that others will put down what they're doing, look at your work, read it, and come back saying: "Yes, this is indeed good."

I suggest that when you open a journal and flip through the pages, you ask yourself: Why do you read some articles and not others?

You'd better write your reports so that when they appear in Physical Review or whatever journal you want, readers won't just flip past those pages—they'll stop and read.

If they don't stop and read, you won't get the recognition you deserve.

Selling your work requires mastering three things.

First, learn to write clearly and well, so people want to read. Second, learn to give relatively formal presentations. Third, learn to express yourself in informal settings.

We had many so-called "backroom scientists." At meetings, they never said a word. Three weeks after a decision was made, they'd submit a report explaining why another approach should have been taken.

But by then, it was too late.

When discussion was hottest and things were moving forward, they wouldn't stand up on the spot and say: "We should do it this way, and here are the reasons."

Besides prepared speeches, you must master this kind of communication.

When I first started speaking, I was so nervous I nearly became physically ill.

I realized: either learn to speak comfortably, or in some way limit my entire career.

The first time IBM invited me to give an evening talk in New York, I decided I had to do it really well, speaking on what the audience truly needed: not a narrow technical topic, but a broader subject.

If they liked it, I would gently add at the end: "I'm always available to come whenever you'd like."

As a result, I got many opportunities to speak to small audiences, and overcame my fear.

Furthermore, I could use this to study: what works and what doesn't.

At conferences, I also kept observing: why are some papers remembered, while most are not?

Technical people always want to give very narrowly scoped technical talks. But most of the time, audiences want broader presentations—they want far more overview and background than speakers are willing to provide.

As a result, many talks are ineffective.

The speaker states the title and immediately plunges into the details of what they solved. The number of people in the audience who can follow may be vanishingly small.

You should first sketch the overall picture, explain why this matters, and then gradually introduce what you did.

That way, more people will say: "Yes, Joe did that." Or: "Mary did that, and I really understand where it fits in the whole field. Mary gave a great talk; I understand what she did."

People tend to give narrow, safe talks, but they usually don't work well. Also, many talks cram in too much information.

So I say, the importance of selling your work is obvious.

Let me summarize: you must work on important problems.

I won't claim it's all luck, but I admit luck plays a significant part. I agree with Pasteur: "Chance favors the prepared mind."

I strongly endorse my own past practice: for years, every Friday afternoon, I spent thinking about big problems. That meant dedicating ten percent of my time to understanding the larger questions in my field, figuring out what mattered and what didn't.

Earlier on, I found myself believing one direction was important, yet spending an entire week working in another direction. That was rather foolish.

If I truly believed the worthwhile work lay over there, why was I heading this way?

Either change the goal, or change what you're doing.

So I changed some of my practices and started moving toward what I considered important. That simple.

Getting Your Boss to Understand

Now, you might say you have no control over what you work on.

That may be true when you're just starting out. But once you've achieved some results, more people will be demanding your output than you can handle. At that point, you have some choice—not complete choice, but some.

Let me tell a story. This also involves how to get your boss to understand.

I once had a boss named Shelkunov. We were good friends then, and still are.

One time, a military man came to me demanding answers to several questions by Friday. But I had already allocated my computing resources to a group of scientists to help them process data in a timely manner. I was swamped with short but important problems.

The military man insisted I handle his matter before Friday's close of business.

I said: "No, Monday. I can work on it over the weekend, but not now."

He went to my boss. Shelkunov told me: "You have to do this for him. He needs it Friday."

I asked: "Why do I have to?"

He said: "You just do."

I said: "All right, Sergei. But Friday afternoon, you must stay in your office, take the late bus home, and watch this man walk out the door with your own eyes."

Late Friday afternoon, I handed the answers to the military man, then went to Shelkunov's office and sat down.

When the man walked out, I said: "See, Shelkunov? Nothing under his arm. Yet I clearly gave him the answers."

Monday morning, Shelkunov called him: "Did you come in over the weekend?"

I could almost hear the pause on the other end. The man was calculating what would happen, but he knew that coming in meant signing in, and it was better not to lie about not having been there. So he admitted he hadn't.

From then on, Shelkunov said to me: "You set the deadlines. You can adjust them."

One lesson like that was enough to get my boss to understand: why I didn't want to take on large tasks that would crowd out exploratory research, why I had grounds to refuse urgent requests that would consume all my scientific computing resources.

I preferred to use those machines to compute large numbers of small problems.

This was still early days, when my computing power was very limited. And in my field, people obviously thought: "Mathematicians don't need machines."

But I needed more computing resources.

Whenever I had to tell scientists from other fields: "No, I can't do it. Not enough computing power," they would complain.

I'd say: "Go tell your vice president that Hamming needs more computing resources."

After a while, I saw what was happening upstairs: many people were telling my vice president, "That man of yours needs more computing resources."

That's how I got it!

I did something else too.

In the early days of computing, whenever I lent out our limited programming staff to help others, I would say: "Our programmers don't get proper credit. When you publish your paper, you must acknowledge that programmer, or don't expect help from me again. You must put her name in. She put in a lot of effort."

I waited a few years, then went through an entire year of the Bell System Technical Journal (BSTJ) and counted what fraction of articles acknowledged some programmer.

I showed my boss the results and said: "This is how central computing work is at Bell Labs. If you think this journal matters, then computing work matters this much."

He had to accept it.

You can get your boss to understand these things, though it's hard.

Today, I'm just looking from the bottom up, not the top down. But I'm telling you: even with resistance from upper management, you can get what you need.

You still need to sell your ideas to them too.

Is It Worth Becoming a First-Rate Scientist?

Now, I want to address a question: "Is it worth making this effort to become a great scientist?"

To answer it, you have to ask those who've done it.

When you get them to drop their modesty, most will say: "Yes, doing truly first-class work, and knowing it's first-class—that feeling is like fine wine, beautiful women, and song all rolled into one." If the respondent is a woman, she'll substitute "beautiful men" for "beautiful women."

Look at those bosses—they always come running back, or demand reports, wanting to be present at the moment of discovery. They're always in the way.

Those who've experienced it want to experience it again.

Of course, this is a limited survey. I never dared ask those who didn't do great work how they felt about it. The sample is biased.

But I still believe it's worth striving for. Working to do first-rate work is absolutely worth it.

Because in the end, the value lies more in the striving than in the final result. The effort to achieve something is itself worthwhile.

Success and fame, in my view, are more like extra bonuses.

I've told you how to do it. If it's so simple, why do so many brilliant people still fail?

For example, to this day, I still believe that quite a few people in Bell Labs' mathematics department were more capable than me, with better talent, yet they produced less than I did.

Of course, some produced more than me. Shannon produced more than me, and some others did a great deal too. But compared to many people with better circumstances than mine, my output was quite high.

Why is that? What problems did they encounter? Why do so many promising people ultimately fail to realize their potential?

One reason is drive and commitment.

Some people with slightly lesser ability throw themselves in completely, and end up accomplishing more than those with high ability who only dabble.

The latter work during the day, go home and do other things, come back the next day. They lack that deep commitment, and truly first-rate work obviously requires it.

They too produce a lot of good work. But remember, we're talking about first-rate work—there's a difference.

Good people, talented people, can almost always do decent work. But we're talking about outstanding work, the kind that wins Nobel Prizes and broad recognition.

Learning to Work with the Organization

A second reason, I believe, is character defects.

Let me give an example of someone I knew at Irvine. He had been head of a computing center and was temporarily serving as special assistant to the university president. Clearly, this was a position with good prospects.

One time, he took me to his office to show me how he handled correspondence and mail. He kept pointing out how inefficient his secretary was.

All the letters were piled around him. He knew where everything was. He would type the letters himself on a word processor.

He was quite proud of how wonderful this system was; without a secretary getting in the way, he could get far more done.

Later, I spoke with the secretary behind his back.

The secretary said: "Of course I can't help him. His mail never reaches me. He won't let me log it in, and I don't know where he's put things on the floor. Of course I can't help him."

So I went to him and said: "Look, if you keep doing things this way, doing everything yourself, you'll only get as far as one person can get. If you learn to work with the whole organization, you can get as far as the organization can support you."

He never advanced further.

His character defect was wanting to control everything himself, unwilling to admit that you need the support of the entire organization.

You'll see this again and again.

Good scientists fight the system rather than learning to work with it, to use everything it can offer. If you learn to use it, it can actually offer a great deal.

This takes patience, but you can learn to use the system well, and you can learn to get around its obstacles.

After all, if you want a "no," just ask your boss—it's easy to get.

If you want to do something, don't ask—do it. Put the fait accompli before him. Don't give him the chance to say "no."

But if you want a "no," that's all too easy.

Don't Let Personality Drain Your Energy

Another character defect is having to prove "I'll do it my way." This time I'll use my own experience.

I came here from Los Alamos. In the early days, we were just renting machine time at 590 Madison Avenue in New York.

At that time, I was still wearing Western-style clothes—big slanted pockets, bolo ties, and so on.

I vaguely felt I wasn't getting the same service as others. So I started watching and comparing. Everyone had to wait their turn, but I felt I wasn't being treated fairly.

I asked myself: "Why? No IBM vice president said 'Give Hamming a hard time.' It's the secretaries at the lower level who actually do this. When machine time opens up, they quickly find someone to slip in, but they always find someone else. Why? I haven't been bad to them."

The answer: my dress didn't match their expectations of someone in this position. Ultimately, I was dressed inappropriately.

I had to choose: continue asserting my individuality, wear whatever I wanted, and let it constantly drain energy that should go into professional work; or conform somewhat more to convention in appearance?

I decided to put a little effort into looking more appropriate.

Once I did, the service I got immediately improved. Now I'm a somewhat eccentric old man, and I get better service than others.

You should dress according to your audience's expectations.

If I were to speak at MIT's computing center, I'd wear a bolo tie and an old corduroy jacket, or something similar.

I at least understand that you shouldn't let clothing, appearance, and manner get in the way of what you truly care about.

But many scientists feel they must assert their individuality, must do things their way.

They have to be able to do this, that, or something else. And they keep paying for it.

John Tukey almost always dressed very casually.

He'd walk into some important person's office, and it would often take a long time before the person realized: this is a first-rate person, I should listen carefully to what he says.

For a long time, Tukey had to overcome this hostility. That was wasted effort!

I'm not saying you should conform in everything. What I'm saying is: being appropriately conventional in appearance can take you much further.

If you choose to assert yourself on everything, always saying "I'll do it my way," you'll keep paying a small price throughout your entire career.

Accumulated over a lifetime, this becomes a huge amount of completely unnecessary trouble.

I put a little effort into telling jokes to secretaries, being a bit friendlier, and got excellent assistance as a result.

For example, once, for some absurd reason, all the copying services at Murray Hill were too busy to help. Don't ask me how that happened, but it did.

I had some documents I urgently needed copied. My secretary called Holmdel, got in the company car, spent an hour driving over, copied the materials for me, and brought them back.

That was the return on my past investment of effort — telling her jokes, being friendly. It was that little bit of extra effort that later helped me.

When you realize you need to draw on the whole organization, and you study how to get it to help you do your work, you gradually learn to make the system serve your needs.

Of course, you could spend your whole life fighting it, waging a small war that never gets formally declared.

I think John Tukey paid a far higher price than he needed to.

He was a genius regardless. But I believe things could have been much better and much simpler for him if he'd been willing to go along with convention just a little, instead of asserting himself at every turn.

He always had to dress the way he wanted.

And it wasn't just clothing — it was a thousand other things. People just keep fighting the system.

Of course, I'm not saying you should never rebel!

Once, the library moved from the middle of the Murray Hill campus all the way to the far end. A friend of mine applied for a bicycle.

The organization wasn't stupid. After a while, they sent him back a campus map and said: "Please mark which routes you plan to take, so we can get you the appropriate insurance."

A few weeks later, they asked again: "Where are you going to store the bicycle? How will you lock it? We'll need to process this and that paperwork for that."

Eventually, he realized they'd bury him in red tape, and he gave up.

He later rose all the way to become president of Bell Labs.

Barney Oliver was a good man. He once wrote a letter to the IEEE.

At the time, Bell Labs had fixed shelf heights, and the IEEE Transactions were taller than those shelves. Since the shelf dimensions couldn't be changed, he wrote to the people at IEEE in charge of publications.

The letter said: Bell Labs has so many IEEE members, and our shelf height is such-and-such, so the journal should change its size.

He gave it to his boss to sign. Later, a carbon copy with the boss's signature came back, but to this day he doesn't know if the original was ever sent.

I'm not saying you shouldn't make gestures toward reform.

I've studied capable people, and I find they don't let themselves get sucked into wars like this. They push a little, then let it go and get back to their work.

Many second-rate people get caught up in little games of tweaking the system, escalate it into a war, and exhaust themselves on some foolish project.

You might say: "But someone has to change the system."

I agree, someone has to. But which do you want to be: the person who changes the system, or the person who does first-class scientific work? Who do you actually want to be?

When you fight the system, know what you're doing. Know which battles are just for fun, where to stop, and how much energy you're willing to spend on it.

My advice: let someone else do that, and you keep working on becoming a first-class scientist.

Among you, there are probably very few who can both reform the system and become first-class scientists.

On the other hand, we can't always give in. Sometimes moderate resistance is reasonable.

I've observed that almost all scientists enjoy tweaking the system occasionally, purely because it's fun.

After all, you can't be original in just one area and completely unoriginal in everything else. Originality means being different. A scientist capable of original work can't be entirely conventional in other respects.

But many scientists let their quirks on other matters cause far more damage than necessary, paying a price that doesn't match the self-satisfaction they gain.

I'm not against all self-assertion — just some of it.

Another weakness is anger.

Scientists often get angry, but it's not a good way to handle things. Amusement is fine; anger is not. Anger misdirects your energy.

You should go with the flow, seek cooperation, rather than constantly fighting the system.

Know Yourself, Manage Yourself

One more thing: look at the positive side of things, not the negative.

I've already given several examples, and there are many more: by simply changing how I looked at things under given conditions, I turned seemingly unfavorable situations into advantages.

Here's another example. I'm an egotistical person — no doubt about that.

I knew that many people who took sabbaticals to write books never finished on time. So before I left, I told all my friends: "When I come back, this book will definitely be done!"

Yes, it absolutely would be — because I wouldn't be able to face coming back if it wasn't!

I used my own ego to force myself to act the way I wanted. I made a big public commitment, so I had to deliver.

I've repeatedly found that when cornered like a rat in a real trap, with no way out, my capabilities are surprisingly strong.

I've found that even when I have absolutely no idea how to do something, saying "No problem, I'll have the answer for you by Tuesday" often works.

By Sunday night, I'll be thinking desperately: how on earth am I going to deliver by Tuesday?

I often bet my own pride, and sometimes I lose. But as I said, like a rat driven into a corner, I'm amazed at how many times I've done things well.

I think you need to learn to use yourself well. You need to understand how to look at your situation from a different angle to make success more likely.

Human self-deception is extremely, extremely common.

You have countless ways to repackage something, make it look like something else, and convince yourself.

When you ask someone: "Why didn't you do this?" they can always find a thousand excuses.

If you look at the history of science, you'll find that in our era, there are often ten people who were all ready, but we only reward the one who did it first.

The other nine will say: "Actually I had that idea too, I just didn't do it..." and so on, plenty of excuses.

Why weren't you first? Why didn't you get it done?

Don't make excuses. Don't lie to yourself.

I don't mind how many excuses you come up with to explain to others. But to yourself, please be as honest as possible.

If you truly want to become a first-class scientist, you need to understand yourself: your weaknesses, your strengths, and those bad habits, like my ego.

How can you turn disadvantages into advantages?

When you're short-staffed, how can you use that to pivot in a direction that turns out to be exactly where you should have been going all along?

I'll say it again: in studying history, I repeatedly see that successful scientists change their angle on a problem, turning what was originally a defect into an advantage.

To summarize, I believe that many people who had the potential for great achievement ultimately failed, in part because:

They didn't work on important problems; they didn't commit emotionally; they didn't try to transform intractable situations into different, more manageable but still important problems; and they kept making excuses for their inaction.

They always said it was luck.

I've told you how simple this can be, and I've told you how to change yourself.

So go — become great scientists!

Q&A

A. G. Chynoweth: Those fifty minutes have condensed the wisdom and observations accumulated over an extraordinary career. There are so many insights that hit home — I can't even take notes fast enough to catch them all.

Some of them remain remarkably relevant today. Take the matter of getting more computing resources — this morning, several people kept coming to me with exactly that request.

Dick, it's been twenty or thirty years since you said those words, and they still hit the bullseye today.

Every one of us can learn a great deal from your talk. To take just one point: I hope that from now on, I won't see so many closed office doors in the corridors of Bell Communications Research. That observation struck me as particularly interesting.

Thank you, thank you very much, Dick. This has been a wonderful retrospective.

Now let's open it up for questions. I'm sure many people want to follow up on some of the points you've raised.

Hamming: Let me first respond to Alan Chynoweth's comment about computing.

At the time, computing was housed in the research department. For ten full years, I kept telling management: "Get that damn machine out of the research department! We're forced to spend all day doing calculations for people, running and operating computers — we can't do any research."

Finally, they listened and decided to move computing out of research.

To put it politely, I became unpopular. Everyone's beloved toy was being taken away, and I was genuinely surprised that nobody kicked me in the shins.

I went into Ed David's office and said: "Ed, you have to leave a machine for the researchers. If you give them a big one, we'll be right back where we started: busy keeping the machine running, with no time to think."

"Give them the smallest machine possible. They're very capable people — they'll learn to solve problems with a small machine, instead of relying on massive computing power."

In my view, that's how UNIX was born.

We gave them a relatively small machine, and they decided to make it do big things. To do that, they had to design a system.

That system was called UNIX!

A. G. Chynoweth: I have to jump in here.

Dick, in our current environment, people have been struggling with red tape attributed to — or actually required by — regulators.

One vice president's assistant, driven to distraction, made a remark that I've quoted repeatedly ever since.

He roared: "UNIX was never a mandated deliverable!"

Bear the Pressure, Keep the Courage

Q: What about personal pressure? Does it seem to have an effect?

Hamming: Yes, of course it does. If you're not emotionally committed, you won't feel it.

For most of my years at Bell Labs, I had early symptoms of ulcers. Later, at the Naval Postgraduate School, I relaxed a bit, and now I'm much better.

But if you want to be a great scientist, you have to endure pressure.

You can live a comfortable life, you can be a nice guy, or you can choose to be a great scientist. But as Leo Durocher said: "Nice guys finish last."

If you want a happy, comfortable life with lots of entertainment and other pleasures, you can certainly have that.

Q: No one would disagree about courage. But for those of us whose hair has already turned gray, or who have already established ourselves, there's not much to worry about.

But I feel that young people today, in this competitive environment, have deep anxiety about taking risks. What advice do you have?

Hamming: Let me quote more of Ed David's views. He was very concerned that our society as a whole is losing courage.

In my view, we have indeed gone through different periods.

After the war, a group of people came out of Los Alamos — where they built the atomic bomb — and out of radar development and other projects, into the mathematics department and research. They had tremendous guts.

They had just seen many things get done, had just won a magnificent war.

We had every reason to be courageous, and so we accomplished a great deal. I can't recreate that environment and make it happen again.

I can't blame this generation for not having that courage. But I agree with your observation — I just can't blame them for it.

I feel that they don't seem to have the desire for great achievement, nor the courage to pursue it. And the reason we had it was that the environment was conducive to developing such courage: we had just come through a war of enormous success.

You all know that for a long time during the war, our situation was terrible — it was a struggle that was almost desperate.

I think the later success gave us courage and confidence.

So from the late 1940s through the 1950s, you would see amazing productivity in the labs, inspired by those earlier experiences.

And many of us had been forced to learn other things, forced to study knowledge we didn't want to learn, forced to open our doors. Later, we were able to use everything we had learned then.

That's simply how it was, and I can't change it. I can't blame today's generation. That's the fact.

Q: Is there anything management can do, or should do?

Hamming: Management can do very little.

If you want to talk about research management, that's an entirely different lecture — I'd need another hour.

What I'm talking about today is: regardless of what management does, and regardless of what other obstacles exist, how can a person still do very successful research.

How? By doing what I observed those people did.

It's that simple, and it's that hard!

Talk with People Who Stimulate You

Q: Should brainstorming be done every day?

Hamming: Brainstorming was very popular for a while, but it doesn't seem to have accomplished much.

For myself, talking with others is very beneficial; but specially organizing a brainstorming session is often not worth it.

I do make special trips to find someone to discuss with, saying: "Look, I think there's something here. What I vaguely see is..." And then we go back and forth.

But you have to pick capable people.

To use another metaphor, you know the concept of "critical mass": enough material, and you reach critical mass.

Also, I mentioned before a concept I call "sound absorbers." When there are too many sound absorbers present, you put out an idea and they just say: "Yeah, yeah, yeah."

What you need is to get that critical mass really working. The other person says: "That reminds me of such-and-such." Or: "Have you thought about this, or that?"

When talking with people, avoid the sound absorbers — they may be very nice people, but they just say "oh, yeah" — and find people who can stimulate you in return.

For example, you couldn't talk with John Pierce without soon being inspired.

I also used to have a group of people I regularly exchanged with, like Ed Gilbert. I would often go to his office, ask questions, listen to him, and come back with new inspiration.

I would carefully choose with whom to bounce ideas around, and with whom not to. Because sound absorbers are a real curse.

They're all good people, they fill up the whole space, but they contribute nothing — they just absorb the ideas. New ideas just disappear, they don't continue to echo.

Yes, I think exchanging with people is necessary.

I think those who work with their doors closed don't do this well, and so they can't get their ideas polished.

For example, someone asks: "Have you noticed that phenomenon over there?" I had no idea before, and now I can go look. Someone has pointed the way for you.

Since coming here this time, I've already found several books I must read when I get home.

As long as I think someone can answer questions and give me clues I don't yet know, I'll seek them out to chat and ask questions. Then I'll go out and look!

Reading and Expression Both Require Method

Q: How do you allocate time and make trade-offs between reading, writing, and actually doing research?

Hamming: I believed early on that the time spent polishing and presenting results should be at least as much as the time spent originally doing the research.

That is, at least fifty percent of the time must be spent on presentation.

That's a very, very large proportion.

Q: How much effort should go to hanging out in libraries, looking up literature?

Hamming: It depends on the field. Let me give an example.

There was a man at Bell Labs who was very, very bright. He was always in the library, reading everything. If you wanted references, you went to him, and he could find you all kinds of materials.

But right as I was forming these ideas, I made a prediction: in the long run, no effect would ever be named after him.

Now, he has retired from Bell Labs and become an adjunct professor. He is valuable, I have no doubt. He has published some very good papers in Physical Review.

But no effect is named after him, because he read too much.

If you're always reading what others have done, you'll think along their lines.

If you want to produce different, new ideas, do what many creative people do: first get the problem quite clear, then temporarily look at no answers.

First think it through seriously yourself: if it were me, what would I do? Can I change the problem slightly, to make it the question that should really be asked?

So yes, you need to know the research progress. But you should read more to discover what the problems are, not to find ready-made solutions.

Reading is necessary — it lets you know what's happening, what's possible.

But reading to find answers doesn't seem to be the way to do great research.

So my answer has two parts: you must read; but what matters is not how much you read, but how you read.

Q: How do you get something named after you?

Hamming: Do great work.

Let me tell you the story of the Hamming window. I used to give Tukey a hard time.

One day, he called me from Princeton — I was at Murray Hill. I knew he was writing something on power spectra. He asked me, would I mind if he called a certain window function the "hamming window."

I said: "Don't do that, John. You know very well, I only did a small part of it, and you did a lot yourself."

He said: "Yes, Hamming, but you contributed many small things. You deserve some recognition."

So he called it the Hamming window.

Let me say a bit more. I used to tease John about this topic of "true greatness."

I said, true greatness is when your name becomes like ampere, watt, and fourier — the first letter can be written lowercase.

That's how the Hamming window came about.

Q: Dick, could you compare the effectiveness of lectures, writing papers, and writing books?

Hamming: In the short term, if you want to inspire someone tomorrow, papers are very important.

If you want lasting recognition, I think books probably contribute more, because most of us need direction.

In this age of nearly infinite knowledge, we need guidance to find our way.

Let me illustrate what I mean by infinite knowledge.

From Newton's time to now, our knowledge roughly doubles every seventeen years. We basically cope with this growth by continually subdividing specialties.

At this rate, in another 340 years, knowledge will have doubled twenty times — that is, grown to about a million times. Every specialty field today will have split into a million specialty fields.

This can't continue forever. Before we find different tools, this current way of knowledge growth will choke itself off.

I believe what people of the future will truly value are books like this: digesting and organizing existing knowledge, removing duplication, discarding methods that don't work well, and explaining the fundamental ideas behind what we already know.

Public lectures are necessary, private conversations are necessary, papers are also necessary.

But I tend to believe that in the long run, books that know what to leave out are more important than books that try to tell you everything.

Because you don't want to know everything. The standard response people give is: "I don't want to know that much about penguins."

You only want the essence.

Enter New Fields, Start Over

Q: You mentioned that the Nobel Prize and the fame that comes with it can affect some people's careers. Is this a more general problem of reputation? And what can we do about it?

Hamming: Several things can be done.

About every seven years, make a significant shift in your research field, even if not a complete change.

For example, I would regularly move from numerical analysis to hardware, then to software, and so on. Because one's ideas in any one direction will gradually run out.

In a new field, you have to start over like a baby. You're no longer a big shot, you can start fresh again, planting acorns that may one day grow into mighty oaks.

I think Shannon held himself back.

When he left Bell Labs, I said: "Shannon's scientific career is over."

Friends criticized me fiercely for this, saying Shannon was just as smart as ever.

I said: "Yes, he'll be just as smart, but his scientific career is finished."

I do think that's how it turned out later.

You have to change.

After a while, you get tired, and you exhaust your original ideas in one field. Then you need to turn to an adjacent direction.

I'm not saying jump from music to theoretical physics to English literature. I mean, shift directions within your own field, so you don't become rigid.

Forcing everyone to change direction every seven years probably wouldn't work. But if it could be done, I would make it a condition for doing research: with a reasonable definition of "change," switch research directions every seven years; or by the tenth year, management has the right to require you to change.

I would insist on change, and I mean it.

Many older researchers master a set of techniques and just keep using them. They keep going in some direction, which was indeed right at the time.

But the world changes. New directions have appeared, and they're still going in the old direction.

You need to enter a new field and gain new perspectives before your old ideas run out.

You can actively do something about this, but it takes effort and energy.

It takes courage to say "yes, I'm willing to set aside the reputation I've already won."

For example, when error-correcting codes had been developed and the theory established, I said to myself: "Hamming, you're going to stop reading papers in this field, stop paying attention to it entirely. Go try something else, don't coast on past results."

I deliberately refused to stay in that field, even stopped reading papers altogether, to force myself to get the chance to try other things.

I was managing myself, and that's what this whole talk today has been emphasizing.

I know many of my own weaknesses, so I consciously manage myself.

I have many weaknesses, so I also have many problems — in other words, many places where I can start managing.

Choose the Path You Truly Want to Take

Q: Could you compare research and management?

Hamming: If you want to be a great researcher, becoming company president won't achieve that goal. If you want to be company president, that's another matter.

I don't object to being company president, I just don't want to be one myself. I think Ian Ross did a very good job as president of Bell Labs.

I don't object to management, but you have to figure out what you want.

Also, when young, you may aspire to become a great scientist; as you get older, you may change your mind.

One day, I went to ask my supervisor Bode: "Why did you become department head? Why not just be an excellent scientist?"

He said: "Hamming, I have a vision for where mathematics should be at Bell Labs. I found that to make this vision reality, I had to push it. I had to be department head."

If what you want to do can be achieved by yourself alone, then go pursue it.

When your vision exceeds what you can accomplish alone, you need to move into management. The bigger the vision, the further you need to go in management.

If you have a vision for what the whole lab, or the entire Bell System, should look like, then you have to rise to the position where you can make it happen. Pushing from the bottom alone won't get you there.

It depends on your goals and aspirations. And when they change over the course of your life, you have to be ready to change with them.

I chose to avoid management because I preferred doing things I could accomplish on my own. But that was my personal choice, driven by my own preferences.

Everyone has the right to make their own choices. Keep an open mind.

But once you've chosen a path, please — be clear about what you've done, what choice you've made. Don't try to have it both ways.

Q: How important is one's own expectation of themselves? And how important is being in a group where people around you expect great work from you?

Hamming: At Bell Labs, everyone expected me to do good work, and that helped me tremendously.

When everyone expects you to do things well, if you have any self-respect at all, you'll try to do them well.

I think being around first-rate people is enormously valuable. I actively sought out the very best.

Once the physicists' table lost its best people, I left. When I found the chemists' table had become the same way, I left too.

I made an effort to stay with people who were highly capable, so I could learn from them and so they would expect excellent work from me.

I think this conscious management of myself served me far better than just letting things happen.

Q: At the beginning of your talk, you downplayed the importance of luck. But you also seemed to skip over the fortunate circumstances that got you to Los Alamos, Chicago, and Bell Labs.

Hamming: There was certainly some luck.

But on the other hand, I don't know what the alternative branches of my life would have been. Unless you can prove that taking another path would not have led to equal or greater success, I can't really say.

Is the specific thing you end up accomplishing a matter of luck?

For example, when I met Feynman at Los Alamos, I knew he would win a Nobel Prize someday. I didn't know what he would win it for, but I was absolutely certain he would do great work.

Whatever direction the future took, this person was going to produce great results. And later, he did.

It's not that you can only do great work by stumbling into some particular situation by chance. Opportunities come along all the time.

The bucket is full of opportunities. If you're in a situation where you grab one of them, you'll do great work in that direction rather than another.

So, was there luck? Yes, but it's not all luck.

Chance favors the prepared mind, and it favors the prepared person.

But this is no guarantee. I'm not guaranteeing that success will happen.

I would put it this way: Luck changes the probability of success, but the individual still retains some control.

So go — and do great work!

Author: Richard Hamming

Original: https://paulgraham.com/hamming.html Recommended reading

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