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Transcription of the Bell Communications Research
Colloquium Seminar - 'You and Your Research' given by
Richard W. Hamming at MRE on March 7, 1986.
J. F. Kaiser
Bell Communications Research
435 South Street, Room 2E-354
Morristown, NJ 07980
ABSTRACT
As a seminar in the Bell Communications Research Colloquia Series,
Dr. Richard W. Hamming, a Professor at the Naval Postgraduate School
in Monterey, California and a former Bell Labs scientist, gave an interesting
and stimulating talk, `You and Your Research' to an overflow audience
of some 200 Bellcore staff members and visitors at the Morris Research
and Engineering Center on March 7, 1986. This talk centered on Hamming's
observations and research on the question "Why do so few scientists
make significant contributions and so many are forgotten in the long
run?" From his more than forty years of experience, thirty of which
were at Bell Laboratories, he has made a number of direct observations,
asked very pointed questions of scientists about what, how, and why
they did things, studied the lives of great scientists and great contributions,
and has done introspection and studied theories of creativity. The talk
is about what he has learned in terms of the properties of the individual
scientists, their abilities, traits, working habits, attitudes, and
philosophy.
This paper is a transcription of that talk along with the discussions
from the question and answer period.
1. INTRODUCTION
As a seminar in the Bell Communications Research Colloquia Series, Dr.
Richard W. Hamming, a Professor at the Naval Postgraduate School in
Monterey, California and a retired Bell Labs scientist, gave a very
interesting and stimulating talk, `You and Your Research' to an overflow
audience of some 200 Bellcore staff members and visitors at the Morris
Research and Engineering Center on March 7, 1986. This talk centered
on Hamming's observations and research on the question "Why do
so few scientists make significant contributions and so many are forgotten
in the long run?" From his more than forty years of experience,
thirty of which were at Bell Laboratories, he has made a number of direct
observations, asked very pointed questions of scientists about what,
how, and why they did things, studied the lives of great scientists
and great contributions, and has done introspection and studied theories
of creativity. The talk is about what he has learned in terms of the
properties of the individual scientists, their abilities, traits, working
habits, attitudes, and philosophy.
In order to make the information in the talk more widely available,
the tape recording that was made of that talk was carefully transcribed.
This transcription includes the discussions which followed in the question
and answer period. As with any talk, the transcribed version suffers
from translation as all the inflections of voice and the gestures of
the speaker are lost; one must listen to the tape recording to recapture
that part of the presentation. While the recording of Richard Hamming's
talk was completely intelligible, that of some of the questioner's remarks
were not. Where the tape recording was not intelligible I have added
in parentheses my impression of the questioner's remarks. Where there
was a question and I could identify the questioner, I have checked with
each to ensure the accuracy of my interpretation of their remarks.
2. INTRODUCTION OF DR. RICHARD W. HAMMING
As a speaker in the Bell Communications Research Colloquium Series,
Dr. Richard W. Hamming of the Naval Postgraduate School in Monterey,
California, was introduced by Alan G. Chynoweth, Vice President, Applied
Research, Bell Communications Research.
Introduction of Richard W. Hamming
Alan G. Chynoweth
Greetings colleagues, and also to many of our former colleagues from
Bell Labs who, I understand, are here to be with us today on what I
regard as a particularly felicitous occasion. It gives me very great
pleasure indeed to introduce to you my old friend and colleague from
many many years back, Richard Hamming, or Dick Hamming as he has always
been know to all of us.
Dick is one of the all time greats in the mathematics and computer
science arenas, as I'm sure the audience here does not need reminding.
He received his early education at the Universities of Chicago and Nebraska,
and got his Ph.D. at Illinois; he then joined the Los Alamos project
during the war. Afterwards, in 1946, he joined Bell Labs. And that is,
of course, where I met Dick - when I joined Bell Labs in their physics
research organization. In those days, we were in the habit of lunching
together as a physics group, and for some reason this strange fellow
from mathematics was always pleased to join us. We were always happy
to have him with us because he brought so many unorthodox ideas and
views. Those lunches were stimulating, I can assure you.
While our professional paths have not been very close over the years,
nevertheless I've always recognized Dick in the halls of Bell Labs and
have always had tremendous admiration for what he was doing. I think
the record speaks for itself. It is too long to go through all the details,
but let me point out, for example, that he has written seven books and
of those seven books which tell of various areas of mathematics and
computers and coding and information theory, three are already well
into their second edition. That is testimony indeed to the prolific
output and the stature of Dick Hamming.
I think I last met him - it must have been about ten years ago - at
a rather curious little conference in Dublin, Ireland where we were
both speakers. As always, he was tremendously entertaining. Just one
more example of the provocative thoughts that he comes up with: I remember
him saying, "There are wavelengths that people cannot see, there
are sounds that people cannot hear, and maybe computers have thoughts
that people cannot think." Well, with Dick Hamming around, we don't
need a computer. I think that we are in for an extremely entertaining
talk.
3. THE TALK
"You and Your Research"
Dr. Richard W. Hamming
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 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!
(End of the formal part of the talk.)
4. 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?
Answer: 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?
Answer: 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?
Answer: 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?
Answer: 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?
Answer: 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?)
Answer: 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?
Answer: 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?
Answer: 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?
Answer: 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?)
Answer: 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?
Answer: 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.
Answer: 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!
End of the General Research Colloquium Talk
5. BIOGRAPHIC SKETCH OF RICHARD HAMMING
Richard W. Hamming was born February 11, 1915, in Chicago, Illinois.
His formal education was marked by the following degrees: B.S. 1937,
University of Chicago; M.A. 1939, University of Nebraska; and Ph.D.
1942, University of Illinois. His early experience was obtained at Los
Alamos 1945-1946, i.e. at the close of World War II. From there he went
directly to Bell Laboratories where he spent thirty years in various
aspects of computing, numerical analysis, and management of computing,
i.e. 1946-1976. On July 23, 1976 he `moved his office' to the Naval
Postgraduate School in Monterey, California where he teaches, supervises
research, and writes books. He continues an active schedule of lecturing
in seminars and short courses.
While at Bell Laboratories, he took time to teach in Universities,
sometimes locally and sometimes on a full sabbatical leave; these activities
included visiting professorships at New York University, Princeton University
(Statistics), City College of New York, Stanford University, 1960-61,
Stevens Institute of Technology (Mathematics), and the University of
California, Irvine, 1970-71.
Richard Hamming has received a number of awards which include: Fellow,
IEEE, 1968; the ACM Turing Prize, 1968; the IEEE Emanuel R. Piore Award,
1979; Member, National Academy of Engineering, 1980; and the Harold
Pender Award, U. Penn., 1981. In 1987 a major IEEE award was named after
him, namely the Richard W. Hamming Medal, ``For exceptional contributions
to information sciences and systems''; fittingly, he was also the first
recipient of this award, 1988. He was both a Founder and Past President
of ACM, and a Vice Pres. of the AAAS Mathematics Section.
He is probably best known for his pioneering work on error-correcting
codes, his work on integrating differential equations, and the spectral
window which bears his name. His extensive writing has included a number
of important, pioneering, and highly regarded books. These are:
Numerical Methods for Scientists and Engineers, McGraw-Hill, 1962;
Second edition 1973; Reprinted by Dover 1985; translated into Russian
also.
Calculus and the Computer Revolution, Houghton-Mifflin, 1968.
Introduction to Applied Numerical Analysis, McGraw-Hill, 1971.
Computers and Society, McGraw-Hill, 1972.
Digital Filters, Prentice-Hall, 1977; Second edition 1983; Third edition
1989; translated into several European languages.
Coding and Information Theory, Prentice-Hall, 1980; Second edition 1986.
Methods of Mathematics Applied to Calculus, Probability and Statistics,
Prentice-Hall, 856 pp., 1985.
The Art of Probability for Scientists and Engineers, Addison-Wesley,
344 pp., 1991.
The Art of Doing Science and Engineering: Learning to Learn, Gordon
and Breach, 1997.
He continued a very active life as Adjunct Professor, teaching and
writing in the Mathematics and Computer Science Departments at the Naval
Postgraduate School, Monterey, California for another twenty-one years
before he retired to become Professor Emeritus in 1997. He was still
teaching a course in the fall of 1997. Richard Wesley Hamming passed
away unexpectedly on January 7th, 1998. An extensive biography appeared
in The New York Times on January 11th, 1998.
Possibly his best-known quotation:
"The purpose of computing is insight, not numbers."
6. ACKNOWLEDGEMENT
I would like to acknowledge the professional efforts of Donna Paradise
of the Word Processing Center who did the initial transcription of the
talk from the tape recording. She made my job of editing much easier.
The errors of sentence parsing and punctuation are those of mine and
mine alone. Finally I would like to express my sincere appreciation
to Richard Hamming and Alan Chynoweth for all of their help in bringing
this transcription to its present readable state.
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