A Talk by Richard Hamming

Richard Hamming was one of the great scientists in the last century. Here is a small talk given by him, touching various issues related to 
research. I found the talk interesting, so have put it there. 
 

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

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

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

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

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

In order to get to the second stage, I have to drop modesty and talk in
the first person about what I've seen, what I've done, and what I've
heard. I'm going to talk about people, some of whom you know, and I
trust that when we leave, you won't quote me as saying 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 is done by luck. It's all a
matter of luck. Well, consider Einstein. Note how many different things
he did that were good. Was it all luck? Wasn't it a little too
repetitive? Consider Shannon. He didn't do just information theory.
Several years before, he did some other good things and some which are
still locked up in the security of cryptography. He did many good things.

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

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

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

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

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

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

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

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

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

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

I give you a story from my own private life. Early on it became evident
to me that Bell Laboratories was not going to give me the conventional
acre of programming people to program computing machines in absolute
binary. It was clear they weren't going to. But that was the way
everybody did it. I could go to the West Coast and get a job with the
airplane companies without any trouble, but the exciting people were at
Bell Labs and the fellows out there in the airplane companies were not.
I thought for a long while about, ``Did I want to go or not?'' and I
wondered how I could get the best of two possible worlds. I finally said
to myself, ``Hamming, you think the machines can do practically
everything. Why can't you make them write programs?'' What appeared at
first to me as a defect forced me into automatic programming very early.
What appears to be a fault, often, by a change of viewpoint, turns out
to be one of the greatest assets you can have. But you are not likely to
think that when you first look the thing and say, ``Gee, I'm never going
to get enough programmers, so how can I ever do any great programming?''

And there are many other stories of the same kind; Grace Hopper has
similar ones. I think that if you look carefully you will see that often
the great scientists, by turning the problem around a bit, changed a
defect to an asset. For example, many scientists when they found they
couldn't do a problem finally began to study why not. They then turned
it around the other way and said, ``But of course, this is what it is''
and got an important result. So ideal working conditions are very
strange. The ones you want aren't always the best ones for you.

Now for the matter of drive. You observe that most great scientists have
tremendous drive. I worked for ten years with John Tukey at Bell Labs.
He had tremendous drive. One day about three or four years after I
joined, I discovered that John Tukey was slightly 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 my age know as much as John
Tukey does?'' He leaned back in his chair, put his hands behind his
head, grinned slightly, and said, ``You would be surprised Hamming, how
much you would know if you worked as hard as he did that many years.'' I
simply slunk out of the office!

What Bode was saying was this: ``Knowledge and productivity are like
compound interest.'' Given two people of approximately the same ability
and one person who works ten percent more than the other, the latter
will more than twice outproduce the former. The more you know, the more
you learn; the more you learn, the more you can do; the more you can do,
the more the opportunity - it is very much like compound interest. I
don't want to give you a rate, but it is a very high rate. Given two
people with exactly the same ability, the one person who manages day in
and day out to get in one more hour of thinking will be tremendously
more productive over a lifetime. I took Bode's remark to heart; I spent
a good deal more of my time for some years trying to work a bit harder
and I found, in fact, I could get more work done. I don't like to say it
in front of my wife, but I did sort of neglect her sometimes; I needed
to study. You have to neglect things if you intend to get what you want
done. There's no question about this.

On this matter of drive Edison says, ``Genius is 99% perspiration and 1%
inspiration.'' He may have been exaggerating, but the idea is that solid
work, steadily applied, gets you surprisingly far. The steady
application of effort with a little bit more work, /intelligently
applied/ is what does it. That's the trouble; drive, misapplied, doesn't
get you anywhere. I've often wondered why so many of my good friends at
Bell Labs who worked as hard or harder than I did, didn't have so much
to show for it. The misapplication of effort is a very serious matter.
Just hard work is not enough - it must be applied sensibly.

There's another trait on the side which I want to talk about; that trait
is ambiguity. It took me a while to discover its importance. Most people
like to believe something is or is not true. Great scientists tolerate
ambiguity very well. They believe the theory enough to go ahead; they
doubt it enough to notice the errors and faults so they can step forward
and create the new replacement theory. If you believe too much you'll
never notice the flaws; if you doubt too much you won't get started. It
requires a lovely balance. But most great scientists are well aware of
why their theories are true and they are also well aware of some slight
misfits which don't quite fit and they don't forget it. Darwin writes in
his autobiography that he found it necessary to write down every piece
of evidence which appeared to contradict his beliefs because otherwise
they would disappear from his mind. When you find apparent flaws you've
got to be sensitive and keep track of those things, and keep an eye out
for how they can be explained or how the theory can be changed to fit
them. Those are often the great contributions. Great contributions are
rarely done by adding another decimal place. It comes down to an
emotional commitment. Most great scientists are completely committed to
their problem. Those who don't become committed seldom produce
outstanding, first-class work.

Now again, emotional commitment is not enough. It is a necessary
condition apparently. And I think I can tell you the reason why.
Everybody who has studied creativity is driven finally to saying,
``creativity comes out of your subconscious.'' Somehow, suddenly, there
it is. It just appears. Well, we know very little about the
subconscious; but one thing you are pretty well aware of is that your
dreams also come out of your subconscious. And you're aware your dreams
are, to a fair extent, a reworking of the experiences of the day. If you
are deeply immersed and committed to a topic, day after day after day,
your subconscious has nothing to do but work on your problem. And so you
wake up one morning, or on some afternoon, and there's the answer. For
those who don't get committed to their current problem, the subconscious
goofs off on other things and doesn't produce the big result. So the way
to manage yourself is that when you have a real important problem you
don't let anything else get the center of your attention - you keep your
thoughts on the problem. Keep your subconscious 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 eat at the physics table. I
had been eating with the mathematicians and I found out that I already
knew a fair amount of mathematics; in fact, I wasn't learning much. The
physics table was, as he said, an exciting place, but I think he
exaggerated on how much I contributed. It was very interesting to listen
to Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay and other
people, and I was learning a lot. But unfortunately a Nobel Prize came,
and a promotion came, and what was left was the dregs. Nobody wanted
what was left. Well, there was no use eating with them!

Over on the other side of the dining hall was a chemistry table. I had
worked with one of the fellows, Dave McCall; furthermore he was courting
our secretary at the time. I went over and said, ``Do you mind if I join
you?'' They can't say no, so I started eating with them for a while. And
I started asking, ``What are the important problems of your field?'' And
after a week or so, ``What important problems are you working on?'' And
after some more time I came in one day and said, ``If what you are doing
is not important, and if you don't think it is going to lead to
something important, why are you at Bell Labs working on it?'' I wasn't
welcomed after that; I had to find somebody else to eat with! That was
in the spring.

In the fall, Dave McCall stopped me in the hall and said, ``Hamming,
that remark of yours got underneath my skin. I thought about it all
summer, i.e. what were the important problems in my field. I haven't
changed my research,'' he says, ``but I think it was well worthwhile.''
And I said, ``Thank you Dave,'' and went on. I noticed a couple of
months later he was made the head of the department. I noticed the other
day he was a Member of the National Academy of Engineering. I noticed he
has succeeded. I have never heard the names of any of the other fellows
at that table mentioned in science and scientific circles. They were
unable to ask themselves, ``What are the important problems in my field?''

If you do not work on an important problem, it's unlikely you'll do
important work. It's perfectly obvious. Great scientists have thought
through, in a careful way, a number of important problems in their
field, and they keep an eye on wondering how to attack them. Let me warn
you, `important problem' must be phrased carefully. The three
outstanding problems in physics, in a certain sense, were never worked
on while I was at Bell Labs. By important I mean guaranteed a Nobel
Prize and any sum of money you want to mention. We didn't work on (1)
time travel, (2) teleportation, and (3) antigravity. They are not
important problems because we do not have an attack. It's not the
consequence that makes a problem important, it is that you have a
reasonable attack. That is what makes a problem important. When I say
that most scientists don't work on important problems, I mean it in that
sense. The average scientist, so far as I can make out, spends almost
all his time working on problems which he believes will not be important
and he also doesn't believe that they will lead to important problems.

I spoke earlier about planting acorns so that oaks will grow. You can't
always know exactly where to be, but you can keep active in places where
something might happen. And even if you believe that great science is a
matter of luck, you can stand on a mountain top where lightning strikes;
you don't have to hide in the valley where you're safe. But the average
scientist does routine safe work almost all the time and so he (or she)
doesn't produce much. It's that simple. If you want to do great work,
you clearly must work on important problems, and you should have an idea.

Along those lines at some urging from John Tukey and others, I finally
adopted what I called ``Great Thoughts Time.'' When I went to lunch
Friday noon, I would only discuss great thoughts after that. By great
thoughts I mean ones like: ``What will be the role of computers in all
of AT&T?'', ``How will computers change science?'' For example, I came
up with the observation at that time that nine out of 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 be reversed, i.e. nine out
of ten experiments would be done on the computer and one in ten in the
lab. They knew I was a crazy mathematician and had no sense of reality.
I knew they were wrong and they've been proved wrong while I have been
proved right. They built laboratories when they didn't need them. I saw
that computers were transforming science because I spent a lot of time
asking ``What will be the impact of computers on science and how can I
change it?'' I asked myself, ``How is it going to change Bell Labs?'' I
remarked one time, in the same address, that more than one-half of the
people at Bell Labs will be interacting closely with computing machines
before I leave. Well, you all have terminals now. I thought hard about
where was my field going, where were the opportunities, and what were
the important things to do. Let me go there so there is a chance I can
do important things.

Most great scientists know many important problems. They have something
between 10 and 20 important problems for which they are looking for an
attack. And when they see a new idea come up, one hears them say ``Well
that bears on this problem.'' They drop all the other things and get
after it. Now I can tell you a horror story that was told to me but I
can't vouch for the truth of it. I was sitting in an airport talking to
a friend of mine from Los Alamos about how it was lucky that the fission
experiment occurred over in Europe when it did because that got us
working on the atomic bomb here in the US. He said ``No; at Berkeley we
had gathered a bunch of data; we didn't get around to reducing it
because we were building some more equipment, but if we had reduced that
data we would have found fission.'' They had it in their hands and they
didn't pursue it. They came in second!

The great scientists, when an opportunity opens up, get after it and
they pursue it. They drop all other things. They get rid of other things
and they get after an idea because they had already thought the thing
through. Their minds are prepared; they see the opportunity and they go
after it. Now of course lots of times it doesn't work out, but you don't
have to hit many of them to do some great science. It's kind of easy.
One of the chief tricks is to live a long time!

Another trait, it took me a while to notice. I noticed the following
facts about people who work with the door open or the door closed. I
notice that if you have the door to your office closed, you get more
work done today and tomorrow, and you are more productive than most. But
10 years later somehow you don't know quite know what problems are worth
working on; all the hard work you do is sort of tangential in
importance. He who works with the door open gets all kinds of
interruptions, but he also occasionally gets clues as to what the world
is and what might be important. Now I cannot prove the cause and effect
sequence because you might say, ``The closed door is symbolic of a
closed mind.'' I don't know. But I can say there is a pretty good
correlation between those who work with the doors open and those who
ultimately do important things, although people who work with doors
closed often work harder. Somehow they seem to work on slightly the
wrong thing - not much, but enough that they miss fame.

I want to talk on another topic. It is based on the song which I think
many of you know, ``It ain't what you do, it's the way that you do it.''
I'll start with an example of my own. I was conned into doing on a
digital computer, in the absolute binary days, a problem which the best
analog computers couldn't do. And I was getting an 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 it and every analog
installation is going to want the report to see if they can't find flaws
in it.'' I was doing the required integration by a rather 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 the answer; it was to demonstrate
for the first time, and beyond question, that I could beat the analog
computer on its own ground with a digital machine. I reworked the method
of solution, created a theory which was nice and elegant, and changed
the way we computed the answer; the results were no different. The
published report had an elegant method which was later known for years
as ``Hamming's Method of Integrating Differential Equations.'' It is
somewhat obsolete now, but for a while it was a very good method. By
changing the problem slightly, I did important work rather than trivial
work.

In the same way, when using the machine up in the attic in the early
days, I was solving one problem after another after another; a fair
number were successful and there were a few failures. I went home one
Friday after finishing a problem, and curiously enough I wasn't happy; I
was depressed. I could see life being a long sequence of one problem
after another after another. After quite a while of thinking I decided,
``No, I should be in the mass production of a variable product. I should
be concerned with /all/ of next year's problems, not just the one in
front of my face.'' By changing the question I still got the same kind
of results or better, but I changed things and did important work. I
attacked the major problem - How do I conquer machines and do all of
next year's problems when I don't know what they are going to be? How do
I prepare for it? How do I do this one so I'll be on top of it? How do I
obey Newton's rule? He said, ``If I have seen further than others, it is
because I've stood on the shoulders of giants.'' These days we stand on
each other's feet!

You should do your job in such a fashion that others can build on top of
it, so they will indeed say, ``Yes, I've stood on so and so's shoulders
and I saw further.'' The essence of science is cumulative. By changing a
problem slightly you can often do great work rather than merely good
work. Instead of attacking isolated problems, I made the resolution that
I would never again solve an isolated problem except as characteristic
of a class.

Now if you are much of a mathematician you know that the effort to
generalize often means that the solution is simple. Often by stopping
and saying, ``This is the problem he wants but this is characteristic of
so and so. Yes, I can attack the whole class with a far superior method
than the particular one because I was earlier embedded in needless
detail.'' The business of abstraction frequently makes things simple.
Furthermore, I filed away the methods and prepared for the future problems.

To end this part, I'll remind you, ``It is a poor workman who blames his
tools - the good man gets on with the job, given what he's got, and gets
the best answer he can.'' And I suggest that by altering the problem, by
looking at the thing differently, you can make a great deal of
difference in your final productivity because you can either do it in
such a fashion that people can indeed build on what you've done, or you
can do it in such a fashion that the next person has to essentially
duplicate again what you've done. It isn't just a matter of the job,
it's the way you write the report, the way you write the paper, the
whole attitude. It's just as easy to do a broad, general job as one very
special case. And it's much more satisfying and rewarding!

I have now come down to a topic which is very distasteful; 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; you shouldn't have to do it. The
world is supposed to be waiting, and when you do something great, they
should rush out and welcome it. But the fact is everyone is busy with
their own work. You must present it so well that they will set aside
what they are doing, look at what you've done, read it, and come back
and say, ``Yes, that was good.'' I suggest that when you open a journal,
as you turn the pages, you ask why you read some articles and not
others. You had better write your report so when it is published in the
Physical Review, or wherever else you want it, as the readers are
turning the pages they won't just turn your pages but they will stop and
read yours. If they don't stop and read it, 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 read it, you must learn to
give reasonably formal talks, and you also must learn to give informal
talks. We had a lot of so-called `back room scientists.' In a
conference, they would keep quiet. Three weeks later after a decision
was made they filed a report saying why you should do so and so. Well,
it was too late. They would not stand up right in the middle of a hot
conference, in the middle of activity, and say, ``We should do this for
these reasons.'' You need to master that form of communication as well
as prepared speeches.

When I first started, I got practically physically ill while giving a
speech, and I was very, very nervous. I realized I either had to learn
to give speeches smoothly or I would essentially partially cripple my
whole career. The first time IBM asked me to give a speech in New York
one evening, I decided I was going to give a really good speech, a
speech that was wanted, not a technical one 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, I got a great deal of practice
giving speeches to a limited audience and I got over being afraid.
Furthermore, I could also then study what methods were effective and
what were ineffective.

While going to meetings I had already been studying why some papers are
remembered and most are not. The technical person wants to give a highly
limited technical talk. Most of the time the audience wants a broad
general talk and wants much more survey and background than the speaker
is willing to give. As a result, many talks are ineffective. The speaker
names a topic and suddenly plunges into the details he's solved. Few
people in the audience may follow. You should paint a general picture to
say why it's important, and then slowly give a sketch of what was done.
Then a larger number of people will say, ``Yes, Joe has done that,'' or
``Mary has done that; I really see where it is; yes, Mary really gave a
good talk; I understand what Mary has done.'' The tendency is to give a
highly restricted, safe talk; this is usually ineffective. Furthermore,
many talks are filled with far too much information. So I say this idea
of selling is obvious.

Let me summarize. You've got to work on important problems. I deny that
it is all luck, but I admit there is a fair element of luck. I subscribe
to Pasteur's ``Luck favors the prepared mind.'' I favor heavily what I
did. Friday afternoons for years - great thoughts only - means that I
committed 10% of my time trying to understand the bigger problems in the
field, i.e. what was and what was not important. I found in the early
days I had believed `this' and yet had spent all week marching in `that'
direction. It was kind of foolish. If I really believe the action is
over there, why do I march in 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 thought was important. It's that easy.

Now you might tell me you haven't got control over 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 for results than you can
deliver and you have some power of choice, but not completely. I'll tell
you a story about that, and it bears on the subject 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 to me and demanded some
answers by Friday. Well, I had already dedicated my computing resources
to reducing data on the fly for a group of scientists; I was knee deep
in short, small, important problems. This military person wanted me to
solve his problem by the end of the day on Friday. I said, ``No, I'll
give it to you Monday. I can work on it over the 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 got to have it by Friday.'' I
tell him, ``Why do I?''; he says, ``You have to.'' I said, ``Fine,
Sergei, but you're sitting in your office Friday afternoon catching the
late bus home to watch as this fellow walks out that door.'' I gave the
military person the answers late Friday afternoon. I then went to
Schelkunoff's office and sat down; as the man goes out I say, ``You see
Schelkunoff, this fellow has nothing under his arm; but I gave him the
answers.'' On Monday morning Schelkunoff called him up and said, ``Did
you come in to work over the weekend?'' I could hear, as it were, a
pause as the fellow ran through his mind of what was going to happen;
but he knew he would have had to sign in, and he'd better not say he had
when he hadn't, so he said he hadn't. Ever after that Schelkunoff said,
``You set your deadlines; you can change them.''

One lesson was sufficient to educate my boss as to why I didn't want to
do big jobs that displaced exploratory research and why I was justified
in not doing crash jobs which absorb all the research computing
facilities. I wanted instead to use the facilities to 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, that a ``mathematician
had no use for machines.'' But I needed more machine capacity. 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 ``Go tell /your/
Vice President that Hamming needs more computing capacity.'' After a
while I could see what was happening up there at the top; many people
said to my Vice President, ``Your man needs more computing capacity.'' I
got it!

I also did a second thing. When I loaned what little programming power
we had to help in the early days of computing, I said, ``We are not
getting the recognition for our programmers that they deserve. When you
publish a paper you will thank that programmer or you aren't getting any
more help from me. That programmer is going to 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 fraction thanked some programmer. I took
it into the boss and said, ``That's the central role computing is
playing in Bell Labs; if the BSTJ is important, that's how important
computing is.'' He had to give in. You can educate your bosses. It's a
hard job. In this talk I'm only viewing from the bottom up; I'm not
viewing from the top down. But I am telling you how you can get what you
want in spite of top management. You have to sell your ideas there also.

Well I now come down to the topic, ``Is the effort to be a great
scientist worth it?'' To answer this, you must ask people. When you get
beyond their modesty, most people will say, ``Yes, doing really
first-class work, and knowing it, is as good as wine, women and song put
together,'' or if it's a woman she says, ``It is as good as wine, men
and song put together.'' And if you look at the bosses, they tend to
come back or ask for reports, trying to participate in those moments of
discovery. They're always in the way. So evidently those who have done
it, want to do it again. But it is a limited survey. I have never dared
to go out and ask those who didn't do great work how they felt about the
matter. It's a biased sample, but I still think it is worth the
struggle. I think it is very definitely worth the struggle to try and do
first-class work because the truth is, the value is in the struggle more
than it is in the result. The struggle to make something of yourself
seems to be worthwhile in itself. The success and fame are sort of
dividends, in my opinion.

I've told you how to do it. It is so easy, so why do so many people,
with all their talents, fail? For example, my opinion, to this day, is
that there are in the mathematics department at Bell Labs quite a few
people far more able and far better endowed than I, but they didn't
produce as much. Some of them did produce more than I did; Shannon
produced more than I did, and some others produced a lot, but I was
highly productive against a lot of other fellows who were better
equipped. Why is it so? What happened to them? Why do so many 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 to it, get more done
that those who have great skill and dabble in it, who work during the
day and go home and do other things and come back and work the next day.
They don't have the deep commitment that is apparently necessary for
really first-class work. They turn out lots of good work, but we were
talking, remember, about first-class work. There is a difference. Good
people, very talented people, almost always turn out good work. We're
talking about the outstanding work, the type of work that gets the Nobel
Prize and gets recognition.

The second thing is, I think, the problem of personality 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 on assignment 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 his office one time and showed
me his method of getting letters done and how he took care of his
correspondence. He pointed out how inefficient the secretary was. He
kept all his letters stacked around there; he knew where everything was.
And he would, on his word processor, get the letter out. He was bragging
how marvelous it was and how he could get so much more work done without
the secretary's interference. Well, behind his back, I talked to the
secretary. The secretary said, ``Of course I can't help him; I don't get
his mail. He won't give me the stuff to log in; I don't know where he
puts it on the floor. Of course I can't help him.'' So I went to him and
said, ``Look, if you adopt the present method and do what you can do
single-handedly, you can go just that far and no farther than you can do
single-handedly. If you will learn to work with the system, you can go
as far as the system will support you.'' And, he never went any further.
He had his personality defect of wanting total control and was not
willing to recognize that you need the support of the system.

You find this happening again and again; good scientists will fight the
system rather than learn to work with the system 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 to use 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 and get a `No' easy. If you want
to do something, don't ask, do it. Present him 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 and I'll speak in this case
of my own experience. I came from Los Alamos and in the early days I was
using a machine in New York at 590 Madison Avenue where we merely rented
time. I was still dressing in western clothes, big slash pockets, a bolo
and all those things. I vaguely noticed that I was not getting as good
service as other people. So I set out to measure. You came in and you
waited for your turn; I felt I was not getting a fair deal. I said to
myself, ``Why? No Vice President at IBM said, `Give Hamming a bad time'.
It is the secretaries at the bottom who are doing this. When a slot
appears, they'll rush to find someone to slip in, but they go out and
find somebody else. Now, why? I haven't mistreated them.'' Answer, I
wasn't dressing the way they felt somebody in that situation should. It
came down to just that - I wasn't dressing properly. I had to make the
decision - was I going to assert my ego and dress the way I wanted to
and have it steadily drain my effort from my professional life, or was I
going to appear to conform better? 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 old colorful character, I get better service than other
people.

You should dress according to the expectations of the audience spoken
to. If I am going to give an address at the MIT computer center, I dress
with a bolo and an old corduroy jacket or something else. I know enough
not to let my clothes, my appearance, my manners get in the way of what
I care about. An enormous number of scientists feel they must assert
their ego and do their thing their way. They have got to be able to do
this, that, or the other thing, and they pay a steady price.

John Tukey almost always dressed very casually. He would go into an
important office and it would take a long time before the other fellow
realized that this is a first-class man and he had better listen. For a
long time John has had to overcome this kind of hostility. It's wasted
effort! I didn't say you should conform; I said ``The /appearance of
conforming/ gets you a long way.'' If you chose to assert your ego in
any number of ways, ``I am going to do it my way,'' you pay a small
steady price throughout the whole of your professional career. And this,
over a whole lifetime, adds up to an enormous amount of needless trouble.

By taking the trouble to tell jokes to the secretaries and being a
little friendly, I got superb secretarial help. For instance, one time
for some idiot reason all the reproducing services 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 it reproduced, and then came back. It
was a payoff for the times I had made an effort to cheer her up, tell
her jokes and be friendly; it was that little extra work that later paid
off for me. By realizing you have to use the system and studying how to
get the system to do your work, you learn how to adapt the system to
your desires. Or you can fight it steadily, as a small undeclared war,
for the whole of your life.

And I think John Tukey paid a terrible price needlessly. He was a genius
anyhow, but I think it would have been far better, and far simpler, had
he been willing to conform a little bit instead of ego asserting. He is
going to dress the way he wants all of the time. It applies not only to
dress but to a thousand other things; people will continue to fight the
system. Not that you shouldn't occasionally!

When they moved the library from the middle of Murray Hill to the far
end, a friend of mine put in a request for a bicycle. Well, the
organization was not dumb. They waited awhile and sent back a map of the
grounds saying, ``Will you please indicate on this map what paths you
are going to take so we can get an insurance policy covering you.'' A
few more weeks went by. They then asked, ``Where are you going to store
the bicycle and how will it be locked so we can do so and so.'' He
finally realized that of course he was going to be red-taped to death so
he gave in. He rose to be the President of Bell Laboratories.

Barney Oliver was a good man. He wrote a letter one time to the IEEE. At
that time the official shelf space at Bell Labs was so much and the
height of the IEEE Proceedings at that time was larger; and since you
couldn't change the size of the official shelf space he wrote this
letter to the IEEE Publication person saying, ``Since so many IEEE
members were at Bell Labs and since the official space was so high the
journal size should be changed.'' He sent it for his boss's signature.
Back came a carbon with his signature, but he still doesn't know whether
the original was sent or not. I am not saying you shouldn't make
gestures of reform. I am saying that my study of 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 some little twitting of the
system, and carries it through to warfare. He expends his energy in a
foolish project. Now you are going to tell me that 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 the person who does first-class
science? Which person is it that you want to be? Be clear, when you
fight the system and struggle with it, what you are doing, how far to go
out of amusement, and how much to waste your effort fighting the system.
My advice is to let somebody else do it and you get on with becoming a
first-class scientist. Very few of you have the ability to both reform
the system /and/ become a first-class scientist.

On the other hand, we can't always give in. There are times when a
certain amount of rebellion is sensible. I have observed almost all
scientists enjoy a certain amount of twitting the system for the sheer
love of it. What it comes down to basically is that you cannot be
original in one area without having originality in others. Originality
is being different. You can't be an original scientist without having
some other original characteristics. But many a scientist has let his
quirks in other places make him pay a far higher 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 becomes angry, and this is no
way to handle things. Amusement, yes, anger, no. Anger is misdirected.
You should follow and cooperate rather than struggle against the system
all the time.

Another thing you should look for is the positive side of things instead
of the negative. I have already given you several examples, and there
are many, many more; how, given the situation, by changing the way I
looked at it, I converted what was apparently a defect to an asset. I'll
give you another example. I am an egotistical person; there is no doubt
about it. I knew that most people who took a sabbatical to write a book,
didn't finish it on time. So before I left, I told all my friends that
when I come back, that book was going to be done! Yes, I would have it
done - I'd have been ashamed to come back without it! I used my ego to
make myself behave the way I wanted to. I bragged about something so I'd
have to perform. I found out many times, like a cornered rat in a real
trap, I was surprisingly capable. I have found that it paid to say, ``Oh
yes, I'll get the answer for you Tuesday,'' not having any idea how to
do it. By Sunday night I was really hard thinking on how I was going to
deliver by Tuesday. I often 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 think you need to learn to use yourself. I think you need
to know how to convert a situation from one view to another which would
increase the chance of success.

Now self-delusion in humans is very, very common. There are enumerable
ways of you changing a thing and kidding yourself and making it look
some other way. When you ask, ``Why didn't you do such and such,'' the
person has a thousand alibis. If you look at the history of science,
usually these days there are 10 people right there ready, and we pay off
for the person who is there first. The other nine fellows say, ``Well, I
had the idea but I didn't do it and so on and so on.'' There are so many
alibis. Why weren't you first? Why didn't you do it right? Don't try an
alibi. Don't try and kid yourself. You can tell other people all the
alibis you want. I don't mind. But to yourself try to be honest.

If you really want to be a first-class scientist you need to know
yourself, your weaknesses, your strengths, and your bad 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 manpower to move into a direction
when that's exactly what you need to do? I say again that I have seen,
as I studied the history, the successful scientist changed the viewpoint
and what was a defect became an asset.

In summary, I claim that some of the reasons why so many people who have
greatness within their grasp don't succeed are: they don't work on
important problems, they don't become emotionally involved, they don't
try and change what is difficult to some other situation which is easily
done but is still important, and they keep giving themselves alibis why
they don't. They keep saying that it is a matter of luck. I've told you
how easy it is; furthermore I've told you how to reform. Therefore, go
forth and become great scientists!