Readers disclaimer; this shit is too long and It’s not readers friendly na imecopy-pasteiwa apa ndo ujisomee, but if it gets boring wachana nayo! Kasome tweets mapema mapema! Richard Hamming gave this talk in March of 1986. It's one of the best talks I've ever read and has long impacted how I think about spending my time.I try to read it every single month or when i need some inspiration.The talk remains very relevant to date so I thought I'd share it here:
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!
DISCUSSION - QUESTIONS AND ANSWERS
A. G. Chynoweth: Well that was 50 minutes of concentrated wisdom and
observations accumulated over a fantastic career; I lost track of all the
observations that were striking home. Some of them are very very timely. One
was the plea for more computer capacity; I was hearing nothing but that this
morning from several people, over and over again. So that was right on the mark
today even though here we are 20 - 30 years after when you were making similar
remarks, Dick. I can think of all sorts of lessons that all of us can draw from
your talk. And for one, as I walk around the halls in the future I hope I won't
see as many closed doors in Bellcore. That was one observation I thought was
very intriguing.
Thank you very, very much indeed
Dick; that was a wonderful recollection. I'll now open it up for questions. I'm
sure there are many people who would like to take up on some of the points that
Dick was making.
Hamming: First let me respond to Alan Chynoweth about computing.
I had computing in research and for 10 years I kept telling my management,
``Get that !&@#% machine out of research. We are being forced to run
problems all the time. We can't do research because were too busy operating and
running the computing machines.'' Finally the message got through. They were
going to move computing out of research to someplace else. I was persona non
grata to say the least and I was surprised that people didn't kick my shins
because everybody was having their toy taken away from them. I went in to Ed
David's office and said, ``Look Ed, you've got to give your researchers a
machine. If you give them a great big machine, we'll be back in the same
trouble we were before, so busy keeping it going we can't think. Give them the
smallest machine you can because they are very able people. They will learn how
to do things on a small machine instead of mass computing.'' As far as I'm
concerned, that's how UNIX arose. We gave them a moderately small machine and
they decided to make it do great things. They had to come up with a system to
do it on. It is called UNIX!
A. G. Chynoweth: I just have to pick up on that one. In our present
environment, Dick, while we wrestle with some of the red tape attributed to, or
required by, the regulators, there is one quote that one exasperated AVP came
up with and I've used it over and over again. He growled that, ``UNIX was never
a deliverable!''
Question: What about personal stress? Does that seem to make a
difference?
Hamming: Yes, it does. If you don't get emotionally involved,
it doesn't. I had incipient ulcers most of the years that I was at Bell Labs. I
have since gone off to the Naval Postgraduate School and laid back somewhat,
and now my health is much better. But if you want to be a great scientist
you're going to have to put up with stress. You can lead a nice life; you can
be a nice guy or you can be a great scientist. But nice guys end last, is what
Leo Durocher said. If you want to lead a nice happy life with a lot of
recreation and everything else, you'll lead a nice life.
Question: The remarks about having courage, no one could argue
with; but those of us who have gray hairs or who are well established don't
have to worry too much. But what I sense among the young people these days is a
real concern over the risk taking in a highly competitive environment. Do you
have any words of wisdom on this?
Hamming: I'll quote Ed David more. Ed David was concerned about
the general loss of nerve in our society. It does seem to me that we've gone
through various periods. Coming out of the war, coming out of Los Alamos where
we built the bomb, coming out of building the radars and so on, there came into
the mathematics department, and the research area, a group of people with a lot
of guts. They've just seen things done; they've just won a war which was
fantastic. We had reasons for having courage and therefore we did a great deal.
I can't arrange that situation to do it again. I cannot blame the present
generation for not having it, but I agree with what you say; I just cannot
attach blame to it. It doesn't seem to me they have the desire for greatness;
they lack the courage to do it. But we had, because we were in a favorable
circumstance to have it; we just came through a tremendously successful war. In
the war we were looking very, very bad for a long while; it was a very
desperate struggle as you well know. And our success, I think, gave us courage
and self confidence; that's why you see, beginning in the late forties through
the fifties, a tremendous productivity at the labs which was stimulated from
the earlier times. Because many of us were earlier forced to learn other things
- we were forced to learn the things we didn't want to learn, we were forced to
have an open door - and then we could exploit those things we learned. It is
true, and I can't do anything about it; I cannot blame the present generation
either. It's just a fact.
Question: Is there something management could or should do?
Hamming: Management can do very little. If you want to talk about
managing research, that's a totally different talk. I'd take another hour doing
that. This talk is about how the individual gets very successful research done
in spite of anything the management does or in spite of any other opposition.
And how do you do it? Just as I observe people doing it. It's just that simple
and that hard!
Question: Is brainstorming a daily process?
Hamming: Once that was a very popular thing, but it seems not
to have paid off. For myself I find it desirable to talk to other people; but a
session of brainstorming is seldom worthwhile. I do go in to strictly talk to
somebody and say, ``Look, I think there has to be something here. Here's what I
think I see ...'' and then begin talking back and forth. But you want to pick
capable people. To use another analogy, you know the idea called the `critical
mass.' If you have enough stuff you have critical mass. There is also the idea
I used to call `sound absorbers'. When you get too many sound absorbers, you
give out an idea and they merely say, ``Yes, yes, yes.'' What you want to do is
get that critical mass in action; ``Yes, that reminds me of so and so,'' or,
``Have you thought about that or this?'' When you talk to other people, you
want to get rid of those sound absorbers who are nice people but merely say,
``Oh yes,'' and to find those who will stimulate you right back.
For example, you couldn't talk to
John Pierce without being stimulated very quickly. There were a group of other
people I used to talk with. For example there was Ed Gilbert; I used to go down
to his office regularly and ask him questions and listen and come back
stimulated. I picked my people carefully with whom I did or whom I didn't
brainstorm because the sound absorbers are a curse. They are just nice guys;
they fill the whole space and they contribute nothing except they absorb ideas
and the new ideas just die away instead of echoing on. Yes, I find it necessary
to talk to people. I think people with closed doors fail to do this so they
fail to get their ideas sharpened, such as ``Did you ever notice something over
here?'' I never knew anything about it - I can go over and look. Somebody
points the way. On my visit here, I have already found several books that I
must read when I get home. I talk to people and ask questions when I think they
can answer me and give me clues that I do not know about. I go out and look!
Question: What kind of tradeoffs did you make in allocating your
time for reading and writing and actually doing research?
Hamming: I believed, in my early days, that you should spend at
least as much time in the polish and presentation as you did in the original
research. Now at least 50% of the time must go for the presentation. It's a
big, big number.
Question: How much effort should go into library work?
Hamming: It depends upon the field. I will say this about it.
There was a fellow at Bell Labs, a very, very, smart guy. He was always in the
library; he read everything. If you wanted references, you went to him and he
gave you all kinds of references. But in the middle of forming these theories,
I formed a proposition: there would be no effect named after him in the long
run. He is now retired from Bell Labs and is an Adjunct Professor. He was very
valuable; I'm not questioning that. He wrote some very good Physical Review
articles; but there's no effect named after him because he read too much. If
you read all the time what other people have done you will think the way they
thought. If you want to think new thoughts that are different, then do what a
lot of creative people do - get the problem reasonably clear and then refuse to
look at any answers until you've thought the problem through carefully how you
would do it, how you could slightly change the problem to be the correct one.
So yes, you need to keep up. You need to keep up more to find out what the
problems are than to read to find the solutions. The reading is necessary to
know what is going on and what is possible. But reading to get the solutions
does not seem to be the way to do great research. So I'll give you two answers.
You read; but it is not the amount, it is the way you read that counts.
Question: How do you get your name attached to things?
Hamming: By doing great work. I'll tell you the hamming window
one. I had given Tukey a hard time, quite a few times, and I got a phone call
from him from Princeton to me at Murray Hill. I knew that he was writing up
power spectra and he asked me if I would mind if he called a certain window a
``Hamming window.'' And I said to him, ``Come on, John; you know perfectly well
I did only a small part of the work but you also did a lot.'' He said, ``Yes,
Hamming, but you contributed a lot of small things; you're entitled to some
credit.'' So he called it the hamming window. Now, let me go on. I had twitted
John frequently about true greatness. I said true greatness is when your name
is like ampere, watt, and fourier - when it's spelled with a lower case letter.
That's how the hamming window came about.
Question: Dick, would you care to comment on the relative
effectiveness between giving talks, writing papers, and writing books?
Hamming: In the short-haul, papers are very important if you
want to stimulate someone tomorrow. If you want to get recognition long-haul,
it seems to me writing books is more contribution because most of us need
orientation. In this day of practically infinite knowledge, we need orientation
to find our way. Let me tell you what infinite knowledge is. Since from the
time of Newton to now, we have come close to doubling knowledge every 17 years,
more or less. And we cope with that, essentially, by specialization. In the
next 340 years at that rate, there will be 20 doublings, i.e. a million, and
there will be a million fields of specialty for every one field now. It isn't
going to happen. The present growth of knowledge will choke itself off until we
get different tools. I believe that books which try to digest, coordinate, get
rid of the duplication, get rid of the less fruitful methods and present the
underlying ideas clearly of what we know now, will be the things the future
generations will value. Public talks are necessary; private talks are
necessary; written papers are necessary. But I am inclined to believe that, in
the long-haul, books which leave out what's not essential are more important
than books which tell you everything because you don't want to know everything.
I don't want to know that much about penguins is the usual reply. You just want
to know the essence.
Question: You mentioned the problem of the Nobel Prize and the
subsequent notoriety of what was done to some of the careers. Isn't that kind
of a much more broad problem of fame? What can one do?
Hamming: Some things you could do are the following. Somewhere
around every seven years make a significant, if not complete, shift in your
field. Thus, I shifted from numerical analysis, to hardware, to software, and
so on, periodically, because you tend to use up your ideas. When you go to a
new field, you have to start over as a baby. You are no longer the big mukity
muk and you can start back there and you can start planting those acorns which
will become the giant oaks. Shannon, I believe, ruined himself. In fact when he
left Bell Labs, I said, ``That's the end of Shannon's scientific career.'' I
received a lot of flak from my friends who said that Shannon was just as smart
as ever. I said, ``Yes, he'll be just as smart, but that's the end of his
scientific career,'' and I truly believe it was.
You have to change. You get tired
after a while; you use up your originality in one field. You need to get
something nearby. I'm not saying that you shift from music to theoretical
physics to English literature; I mean within your field you should shift areas
so that you don't go stale. You couldn't get away with forcing a change every
seven years, but if you could, I would require a condition for doing research,
being that you will change your field of research every seven
years with a reasonable definition of what it means, or at the end of 10 years,
management has the right to compel you to change. I would insist on a change
because I'm serious. What happens to the old fellows is that they get a
technique going; they keep on using it. They were marching in that direction
which was right then, but the world changes. There's the new direction; but the
old fellows are still marching in their former direction.
You need to get into a new field to
get new viewpoints, and before you use up all the old ones.
You can do something about this, but it takes effort and energy. It takes
courage to say, ``Yes, I will give up my great reputation.'' For example, when
error correcting codes were well launched, having these theories, I said,
``Hamming, you are going to quit reading papers in the field; you are going to
ignore it completely; you are going to try and do something else other than
coast on that.'' I deliberately refused to go on in that field. I wouldn't even
read papers to try to force myself to have a chance to do something else. I
managed myself, which is what I'm preaching in this whole talk. Knowing many of
my own faults, I manage myself. I have a lot of faults, so I've got a lot of
problems, i.e. a lot of possibilities of management.
Question: Would you compare research and management?
Hamming: If you want to be a great researcher, you won't make
it being president of the company. If you want to be president of the company,
that's another thing. I'm not against being president of the company. I just
don't want to be. I think Ian Ross does a good job as President of Bell Labs.
I'm not against it; but you have to be clear on what you want. Furthermore,
when you're young, you may have picked wanting to be a great scientist, but as
you live longer, you may change your mind. For instance, I went to my boss,
Bode, one day and said, ``Why did you ever become department head? Why didn't
you just be a good scientist?'' He said, ``Hamming, I had a vision of what
mathematics should be in Bell Laboratories. And I saw if that vision was going
to be realized, I had to make it happen; I had
to be department head.'' When your vision of what you want to do is what you
can do single-handedly, then you should pursue it. The day your vision, what
you think needs to be done, is bigger than what you can do single-handedly,
then you have to move toward management. And the bigger the vision is, the
farther in management you have to go. If you have a vision of what the whole
laboratory should be, or the whole Bell System, you have to get there to make
it happen. You can't make it happen from the bottom very easily. It depends
upon what goals and what desires you have. And as they change in life, you have
to be prepared to change. I chose to avoid management because I preferred to do
what I could do single-handedly. But that's the choice that I made, and it is
biased. Each person is entitled to their choice. Keep an open mind. But when
you do choose a path, for heaven's sake be aware of what you have done and the
choice you have made. Don't try to do both sides.
Question: How important is one's own expectation or how important
is it to be in a group or surrounded by people who expect great work from you?
Hamming: At Bell Labs everyone expected good work from me - it
was a big help. Everybody expects you to do a good job, so you do, if you've
got pride. I think it's very valuable to have first-class people around. I
sought out the best people. The moment that physics table lost the best people,
I left. The moment I saw that the same was true of the chemistry table, I left.
I tried to go with people who had great ability so I could learn from them and
who would expect great results out of me. By deliberately managing myself, I
think I did much better than laissez faire.
Question: You, at the outset of your talk, minimized or played
down luck; but you seemed also to gloss over the circumstances that got you to
Los Alamos, that got you to Chicago, that got you to Bell Laboratories.
Hamming: There was some luck. On the other hand I don't know
the alternate branches. Until you can say that the other branches would not
have been equally or more successful, I can't say. Is it luck the particular
thing you do? For example, when I met Feynman at Los Alamos, I knew he was
going to get a Nobel Prize. I didn't know what for. But I knew darn well he was
going to do great work. No matter what directions came up in the future, this
man would do great work. And sure enough, he did do great work. It isn't that
you only do a little great work at this circumstance and that was luck, there
are many opportunities sooner or later. There are a whole pail full of
opportunities, of which, if you're in this situation, you seize one and you're
great over there instead of over here. There is an element of luck, yes and no.
Luck favors a prepared mind; luck favors a prepared person. It is not
guaranteed; I don't guarantee success as being absolutely certain. I'd say luck
changes the odds, but there is some definite control on the part of the
individual.
Go forth, then, and do great work!