Questions and answers after the talk by Professor Hamming

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!