Well, this is the last lecture of the course
because the next two meetings,
nominally I will be at Los Alamos giving a talk at a symposium
there. This talk is you and your research.
I've given it many times. It might as well be called you and
your engineering career, or even you and your career in
the discussions afterwards for this talk.
Many times discussions have led that these are broad principles
of success in many fields.
So while I will talk about research, because that's what I've studied,
it's really fairly broadly based.
I've told you earlier about my career, but I'll
remind you, at Los Alamos,
I became aware that I was a janitor of science.
Some of the people who keep the thing going,
but whose opinion does not matter a great deal, they could
trust me to do simple things, but the major decisions I was not really
involved in. And to put it bluntly and
unpleasantly, I was envious,
plain envious. And I began to ask myself,
what's the difference between the really capable
scientist myself and.
I studied it. I went up to Bell Labs, I studied it further. This is
really a report on what I found different between the first
class and the second class. I want to remind you of something which
is not in the notes, what is called the Matthew effect,
named after St. Matthew. There's a verse there in the Bible which
says, unto those who have shall be given unto those
who have not should be taken away. Or put it bluntly,
those with God gets and those who haven't got it. You know what happens,
it's true in science, when you become famous, it's easy
to remain famous. For example, once I became moderately famous, I was invited to
give talks at IBM and so on. And when I went there, they would show
me this or that that's going on, show me the research labs or production
lines and so on. So I got to know more information than the other person.
Once famous, it's very easy to remain famous.
Once not famous. And what you do
do will be taken away from you. So it's necessary to do something outstanding.
Otherwise what you do is sort of taken away from
you, as St. Matthew said. Now, why do I believe
it's important to talk? Because as far as I
know, and as far as you know, you have one life to lead.
You might as well lead a life you would like to have.
And I suggest you a life of doing something significant,
by your definition of significant, is worthwhile
to live a life which you got by in the back. And you say,
well, I didn't do any harm. Is not terribly
satisfactory.
So I am really trying to get you to think about doing
significant things by your definition of significant.
Now I have to talk about my own experience I have throughout the course because
if I talk about other people, it doesn't have the effect. My purpose is to
stick a knife in your back and give it a good twist and make you
say, at the back end, well, if Hamming could do it, why couldn't I?
After all, he's not that much better than I am. He's doubtful if he is
better than you are. So my purpose in telling
direct stories is to make you conscious that you can be at
least as great or better than I was, and I didn't do badly.
Now, I'll start psychologically, rather logically.
The first objection people have is, well, fame is a matter of luck.
I have cited regularly Pasteur's remark, luck favors
a prepared mind. Yes, there is an element of luck.
No, there isn't. For example, when I
met Feynman, he was running computing. I was brought in to
help get him out so he'd go back to physics.
I knew he'd get a Nobel Prize for something. He was one of those
people you could see the man had energy and ability and he was going to
do something. It was in the nature of him to be
something. Well,
yes, luck favor prepared mind. But also it says,
you prepare yourself and then luck hits you. But there's
lots of ways luck can hit you. For example,
when I went to Bell Laboratories, the first months I was
there, Shannon, a lady, Ms. Sally Mead and myself,
shared a very big room in the attic.
Shannon went on to create information theory. I created coding theory.
There were a large number of people around. Yes, it was
in the air, but why did we do it? Why was it
us? Shannon had done other good things before then.
He, in his master's thesis, had observed that Boolean algebra
is what you need for switching circuits. He had made a
number of very significant contributions.
Einstein is famous for writing five papers in one year
in a journal, several of which are very great classics.
It isn't luck. It is two. I gotta
say both it is and it is not.
You prepare yourself the way you lead from day to day,
lead your life from day to day. You prepare yourself for success or
you don't. And when the lightning strikes, you're either ready or you're
not. It misses you or it hits you.
What will be is open to debate. But I think the Shannon had
not created information Theory. He would have done other significant things. He'd done A bunch
before he would do ones afterwards. So I sort
of deny it.
At least I deny it's all luck.
Now, Newton observed, Sir Isaac Newton,
that if other people thought as hard as he did, they would get
the same results. And Edison said, genius is
99% perspiration and 1% inspiration.
And I tell you the same thing to a great extent. It is
constant hard work that does it. Nothing more and
nothing less. The very able people work very hard all
the time. At Los Alamos, on Sundays, when we goofed off
a little bit when they went out hiking in the mountains behind Los Alamos,
they still talk shop.
They were at the problem all the time.
Now, one of the characteristics, but not always, is that when
young they showed a great deal of ability. Newton did not,
as far as I can make out reading biographies. He really didn't look
unusual to anybody until after he came up to Cambridge in college
and his mathematical knowledge was about arithmetic when he came.
He's an exception and a few others. Now,
Einstein considered the fact that after he got
his doctor's degree, he had no legitimate job except for seven years
in the patent office. No job at the university.
He didn't get early recognition, but when he got it, he did
it. And that indicates that the IQs
and such other things which people are supposed to have, it's a helpless.
But quite a few great people don't have fabulously high IQs
as measured by the normal methods.
Einstein certainly did not look like a good student.
Quite many other people didn't. A personal example.
He's dead now, so I can tell you a guy named Bill Fan walked into
my office at Bell Labs and he wanted to do zone melting.
Now, zone melting, you have a bar, you have a coil around it which you
heat by induction. You melt the metal and you
move it down slowly. If the impurities stay in
solution, you drag the impurities down. If the impurities trying to drop out,
they're pushed to the other side and many, many passes removes
the impurities from the middle of the bar.
Well, he has some equations. I put some algebra
on it and some calculus and got some partial answers. But I
could see that he needed computing. Well, I went
around to his department and asked about him. Well, they didn't think much of
him. I go back to my office.
I thought he had a good idea. I had resolved to
work with important people. I want to do important work, work with important
people. Here was my chance to contribute to a really good idea, if it
were good. But his department didn't think Much of
him. But I reflected,
Muhammad had to leave town,
flee for his life. A prophet
is without honor in his own country. Remember, it will be often
true that your local people cannot see that you are doing
great work. I concluded I would help him.
I taught him how to use the machine. I made machine time available to him
and so on. And well, he picked up all kinds of prizes.
He became a famous man. His laboratory
was made a national treasure one time also
along the way, from being inarticulate and knowing little mathematics
and lacking confidence, he became a man who spoke clearly and
well and gained confidence. He had lacked confidence when he was
young. And that success own melting was
his one great idea. But it was what Bell Labs needed and
what everybody else needed. We needed to be make able. We needed
to be able to make germanium without very many impurities.
Then we need to be able to put as many we want in. Because if
you now take the same zone and drag it down, you can drag down impurities
about the density you want in them. You have remarkable control with
zone melting. Now you make 1000 passes or something
and that's why you can't do it numerically other than with
a computing machine, because the thousand passes have end
effects and they bounce around.
So I was right that time. I guessed the man had something
important. I worked with him and I was part of something that was
important. Now, having disposed
of psychological objections of luck and lack of high IQ because
some of you say, well, I wasn't the brightest student in my class, so what?
It doesn't matter. Let's get down to other things.
Now the most important thing probably of great people is
they believe they can do great work. They have confidence in
themselves. If you don't think you do great
work, it's not likely that you're ever going to do it.
It's that simple. Now you can be too overconfident,
but you should have a fair amount of confidence. Take for example, Shannon.
You remember when I did information theory, I pointed out how when stuck
with random codes, he averaged over all random
codes and showed the average was arbitrarily good. Therefore, one good code
had to exist. Who but a man with almost infinite
courage would do that? He had it.
Now I can tell you another way. Simply there was a year or so when
he came in about 10 o'clock, played chess until about 2 and went home
at the end of the year. The company gave him a salary raise, but all
you could see him doing was that at home he was creating information theory.
Well, the way he played chess is the following.
When you are attacking chess, you can either defend yourself or you attack back.
Shannon never defended himself.
He attacked back. And the game would get tied up more and more and more
and more complex. And finally he'd stop and think for a long while,
grab his queen in advance and say, I ain't scared of nothing.
Bingo. The whole game would collapse suddenly because he finally precipitated all the
pending operations and either won or lost.
Well, I learned that expression, I ain't scared nothing.
I've used this several times by myself when stuck. And I didn't know what on
earth to do. I said, hmm, good enough for Shen, good enough for
Hamming. I ain't scared nothing. Let's go ahead and see what happens.
And sometimes by copying his style, I came
through to success. I deliberately copied his
style.
Now, another example.
I hope most people are dead to guess they aren't, but they won't hear this.
I was in a math department, and the math department. We used to
go to lunch together. They played games through boomerangs, flu kites,
and played this and that, and they fiddled around.
And I wanted to succeed. And I said, I can't afford to waste
lunchtimes. So I went around to the physics table, where I had written
a paper with one of the physicists, a good one,
and said, may I join you? Sure, I'm welcome. The table consists
among other people of Bardeen, Shockley and Bratton, the Nobel Prize winners.
J.B. johnson of Johnson, Noyes and some others. My friend among
others. And I used to have lunch with him for years.
I learned a lot. I learned a lot of tricks out of Shockley, how he
did things. I watched other people. I learned how to do
things sensibly. Well, finally, the Nobel Prize came through,
promotion came through, Jobs elsewhere came through. And all
the able people left, including my friend, he had promoted up
the line. Well, what was left was the
dregs. Hardly worth eating lunch with.
But over in the other corner of the dining room was a big table.
The chemists and I had written a paper on nuclear magnetic
resonance with one of the guys. And so I said, do you mind if I
join you? So I sit down and we start talking about chemistry and such other
things for a long while. And finally one
day I walk in and say, if what you're
working on is not important and it's not likely to lead to
important things, why are you working on it?
After that, I ate with the engineers.
That was spring in the fall, going down the long corridor, bell Labs.
My friend chemist stopped me and said, you know,
hamming, that remark of yours got underneath my skin. I've spent the
summer thinking about the important problems in my field. I have not changed my
research, but I think it was well worth the time. I say,
thank you, Dave, and walk on. About two weeks later,
I notice he's made head of the department. About 10
or 12 years ago, I noticed he is a member of the National Academy of
Engineering. I have never heard of
anything about any other person at the chemistry table. Not one.
The one man who could hear if what you are doing
is not important, not likely important, why are you doing it? The one man who
could did become important. He didn't succeed.
The rest of them who couldn't hear didn't.
It's that simple. If you don't
work on important problems, you are not going to do important things. Except by
the dumbest of dumb luck,
you must work on important problems. Now, you can't work on them all the time
because that's what Nobel Prize winners do.
They get a Nobel Prize and they think like Shannon also they
can only work on important problems.
As a result, they don't do anything. You have to plant
little acorns which grow into my oak trees,
but you have to plant the acorns which will grow.
You have to learn the small things. So the great
thing wrong with Nobel Prizes is you now think you can only work on important
problems and you don't. What? You have to work on problems
which can become important and matter which have a future
which will grow into mighty oak trees.
Another thing that ruins the Nobel Prize winner, of course, is everybody gets
famous. You are put in all kinds of committees and all kinds of other things,
and you can't get any work done. They stop you from doing it
by various promotions and so on. So that's a lot of
reasons why Nobel Prize winners often don't do very much afterwards.
Now, confidence in yourself, I said, is important. Overconfidence, of course,
is a disaster. I'll put it as I did the
other day. The difference between being strong willed and stubborn,
the difference between confidence and overconfidence is about the same thing. It's this
fine line. I've seen a lot of people abandon a good idea
too soon. And I've seen people cling to a bad idea too long.
They're both difficult problems.
Now, one of the features which you can cling to regularly is
a desire to do excellent work. Whatever you
do, you're going to do well. Now, it's not true My father said
anything worth doing at all is worth doing well. There are some things you might
as well get rid of. Like you have to sign some paper
for this or that. You sign them. You don't try and write your handwriting,
the most beautiful one you can, you just get rid of it.
But in general, you try and do excellence. This is the one guide I think
you can say whatever I do, I am going to do well.
And that will give you some unity. Because I've talked to you before about
the drunken sailor who staggers a couple steps this way, then a couple this way,
then a couple this way in a total of many, many steps. He gets a
distance to the square root of N. But if there's a pretty girl over
there, he staggers like this, and he staggers like this and he gets a distance
proportional to N. When you have a vision, you will
go a long way. Without a vision of what you're going to do and where
you're going to be, you're not going to get very far.
It's that simple. You have to get a vision of what
you are going to do and be and then pursue it. And excellence
is one of the best tracks you could use. I am going to do things
very well. I'm going to do more than just a good job. I'm going to
do a first class job.
Now, what you may consider good working conditions may not be for you.
It's very sad. But what you think are good working conditions are not.
The example I've given you already is working with a door closed or opener.
If you work with your door closed, you won't be interrupted. You get
your work done. You work with your door open. People come by and stop
and chat and so on and so on. But I've noticed very
clearly at Bell Laboratories, those who work with the door shut may
be working just as hard ten years later. But they don't know what to
work on. They are not connected with reality. Those who had the
door open may very well know what's important.
Now, I cannot prove to you whether the open door
causes the open mind or where the open mind causes the open door.
I suspect a bill. I can only establish the correlation and
it was quite spectacular. Almost always
the guy with the door closed were often very well able, very gifted,
but they seemed to work always on slightly the wrong problem.
So you have to get wide feeling for what is going on. And the
supreme example of this closure is the Institute for Advanced Study in Princeton.
They take in people who've Done something great. They give them luxury, a beautiful office,
a beautiful restaurant to dine in, wonderful grounds and everything
else like that. Adequate salary to live on, no cares, no worries,
no nothing. You're freed for life or anything at all.
What happens? The Balcomb continue working on the problem
that made them famous. They keep on elaborating and so on. Well,
they've already made it famous. It doesn't have to be added to. They got the
thing going. Rarely do they change. Now, Von Neumann was
different. He was at the Institute, and he did go out in reality and
turn up in Washington and other places. He traveled widely and was
receptive to new ideas. But the bulk of the people who got appointed
Institute for Advanced Study don't
keep the door open on life, as it were, and they don't do anything
comparable to what they'd done before. They are very able people, but the
Institute, in my opinion, sterilized them to a great extent.
So what do you think is the ideal working conditions or not?
Now, I'll give you some examples of this.
When we began with the IBM 701 computer, we programmed
in absolute binary, and there were a bunch of these machines in the west coast
airframe companies, and the rest were scattered around.
Now, it became obvious to me that the method the
west coast used for programming, namely we hire an acre of
girls, spread out and they program typically girls,
but sometimes men. But mainly they were programming girls in those days.
Well, it was clear to me Bell Labs would never give me an acre of
girls. They weren't about to do that kind of a
thing. Well, what do I do? I'm in computing.
I want to be in the frontier what everybody else
has. I'm not going to have. Well,
I could quit and get a job on the west coast, probably any one
of airframe companies, because I was wheezing no one out there.
But Bell Labs had a lot of very good people, and the airframe companies have
a few good people scattered widely, but not a high density.
Remember, I'm not trying to learn how to be great, so I'm studying great people.
Bell Labs, a place to study, but the airframe is a place where to get
a tool. So I think for a long while, and one day I said to
myself, hamming, you believe a machine can do anything?
Why don't you make the machine do the programming?
Well, what is the cause? The net effect was that I was put immediately
right in the frontier of programming. How do I make the machine
do the programming force? What appeared to be a defect
by turning the Problem around became an asset.
Grace Hopper has told several other stories in a similar way.
What appears to be a defect is an asset.
So frequently when you think things are wrong
and you haven't got the wherewithal to do it, if you turn the problem around,
you can turn it a great success. Another one is slightly different.
When I was doing this equation I told you
about a Navy intercept plane. I was
solving it on a digital machine because the analog machine outside
of Philadelphia couldn't do the job.
No analog machine at that day could do it because
they didn't have the required accuracy.
Well, I was using a variation of
Mills method, which was pretty crummy. I had found Mill's
method was unstable. I'd patched up a little bit there it was.
One day I realized the following.
I was going to have to fill in a report. Well, I did, because government
contracts always require reports. And everybody
who had an analog computer was going to try and pick flaws in what I
did because I was really showing that a digital
machine could beat the analog on its own home ground.
That's really what I was doing, not getting the answer to the problem. I was
really demonstrating something much more important.
Well, I promptly started deriving a better
method of integrating the differential equations. And I finally used a method
which for some years was known as Hamming's method. I don't recommend it now,
but it was very suitable for the machines as they were. And so I had
the girl programmer change a few of the instructions,
run a trajectory once more to check the new program, got the same as the
old answers, and then went ahead. Thus,
the report has a very jazzy method of solving differential
equations instead of very crummy method. Both were equally effective,
but one was defensible and one was not. You see,
I changed the nature of the problem. I saw that the problem, although it originally
was get the answers to these trajectories, in fact it
was something else. It was proving that a digital machine could beat the analog
machine on its own home ground of differential equations.
I redefined the problem and made
it a success. I would not have
found Hamming method if I had not realized that the method I was using,
which was adequate for me, and we could all see we were getting the right
answer. But it was not nice. It was not clean and simple.
It was rather ugly. So I changed the problem.
Now, these all tell you the conditions you want are seldom realized,
but that you can change the conditions that you have
to make success either by inverting the problem or,
as I told you, the second story, changing the nature of the problem and recognizing
the underlying real problem. Now that's something I've done several times.
There's one very early problem I solved spectacularly successful, not only
on a computing point of view, but from a physics point of view. The value
in the transistor research was extremely valuable. Well,
I meditated over why was that successful. I studied
it over and over again. And I believe the statement,
you should study your successes. You don't study your failures,
study successes, because when your time comes,
you will know how to succeed. If you study failures, you'll know how to fail.
So study success very closely, not only yours, but other people's.
Why did Galileo do what he did? How did Newton do it? Try as best
you can to study other people, how they succeeded,
what were the elements of their success, which elements of that
can you adapt to your personality? You can't be everybody, but you
have to find your own method. And studying success is a
very good way of forming your own style.
Now, one day, I think I told you a
story before. I'll repeat it. One day I found John Tukey, with whom
I was working extensively, was my age, and the guy was clearly a
genius. I went in to our mutual
boss and says, hendrik, how can anybody my age
know so much as John Tookey does? Well,
he leaned back in his chair, grinned at me and said,
hamming, you'd be surprised how much you'd know if you worked as hard as he
did. I slunk out of the
office. There wasn't anything to say, and I stayed home.
When I was home, I thought frequently, I am not working really
as hard as I could. I'll never be able to work as hard as John
does. I haven't got the psychic energy, but I can work a hell of a
lot harder than I have been. Let me reorganize
my life. Let me quit spending my time and
reading nonsense magazines and plumbing through newspapers. They're not very important
to my career. Let's spend my time studying things in my
career. For example, I got appointed deliberately a
book review editor. Therefore, for there's
always a book on my coffee table right next to it waiting to be read
and a review written. When a review was
written by me, I set it aside for a week and asked myself afterwards,
is that a good review? Does that re digest the book? If it doesn't,
you're rereading the book and writing a better review. This way,
I forced myself to get a wide acquaintance in computer science
and being the book review editor I got to review the books I wanted.
This was a device. Now it's true. I quit reading New Yorker.
I quit reading magazines. I quit reading a lot of other things. My wife complained
occasionally. All I looked New Yorker was the jokes. She was
right. I didn't have time to do everything. I wasn't
a first class genius. I had to work hard. So I
simply set aside those other things and did that.
It's not hard to do. You just do it.
Now I want to say another couple of things. The race is not to
the swiftest. The guy who works hardest doesn't
win. The person who works on the right problem at the right time, in the
right way is what counts and nothing else.
That's what I'm trying to do. In this whole course I've been trying to teach
you something about style and taste so you'll be
able to have some hunch of when the problem is ripe,
what problem is ripe and how to go about it.
The right problem at the right time, the right way counts and nothing else counts.
Nothing. You got to do that.
But it's easy. There's a million races being run. You just got to get in
one of them and win.
Now,
I mentioned earlier regarding the chemists about
what are the important problems in your field? At the urging of some other
people, partly and partly in my own, I used to set
aside Friday noon and Friday afternoon for great thoughts.
Meaning, yes, I'll answer telephone, yes, I'll sign a sheet of
paper. But mainly, what is the effect of computing
on science? What the hell am I doing with this computing machine?
How is it going to affect AT and T? What should
I be doing with computing? What is the nature of software?
My friends all, after a while got to know Friday afternoon is great thoughts.
What's the nature of this, that and the other thing? I spent 10% of
my time trying to answer the question, what are the
important problems in my field? 10%. Friday afternoon,
straight through. Don't do it Monday morning because you'll be interrupted
immediately. If you do it Friday afternoon, some of it can linger over on Saturday
and Sunday. If you do it Monday morning, there's a hot conference at 10:00 and
bingo, everything's broken up. I use it Friday afternoon for many,
many years. I recommend that you find a regular time to
stop and think. What are the important things?
What is going on? What is the nature of what you are doing?
What is the characteristic of the job? What are the fundamentals
behind it? So you have some idea where you're headed
so you can march in a uniform direction and get far, rather than being a
drunken sailor and getting nowhere.
And I've regularly, in this picture, tried to stress, in these lectures,
stressed the bigger picture. I've tried to stress fundamentals.
No one knows what the fundamentals will be tomorrow. But you could try to
ask, what are the fundamentals? The things about which other things seem to depend
and those things which seem to be true tomorrow. But maybe not.
I've also stressed the necessity of learning new things.
All kinds of new fields come up endlessly.
They're going to keep on coming up. You have to get some grip on them.
You can't learn them all, but you have to get an idea. Well, that is
relevant to my field. That's interesting, but it isn't relevant. Forget it.
It's a very difficult problem to.
Now there's another thing I have to talk about. Great people. It took me
a long, long while to discover this. After I've
been studying, I'd say 15 or 20 years before I realized the tolerance
of ambiguity they both believe
and disbelieve. Now, most people want to believe something is true or it
isn't true. Great scientists believe the theory
is true enough, so they continue working. Because if you don't believe the
theory is true, you won't. But they disbelieve enough to notice what's wrong and
make the big change to the new theory.
If you believe the theory is right, you won't make the big change
to the next new theory. You won't make the big step forward. You'll merely
elaborate and extend the old theory. And that won't make you
a great scientist. It'll make you just a good one, which I'm not complaining about.
But greatness consists of seeing what other people
have missed and seizing upon the contradictions and making the
new step forward. You have to
tolerate ambiguity. And I have not the faintest idea how I'd ever teach
a course in ambiguity. I've thought about it many times.
How would I put a course together to teach students to tolerate ambiguity?
I haven't a clue, so I don't know what to do.
I really tell you, the tolerance of ambiguity, not being so certain
everything is correct, is a necessary feature.
Now, most great scientists have 10 to 20 problems in their minds,
one just hanging around, which when they get a clue how
to attack, they drop other things and rush into that problem and finish it off
first. Something between 10 and 20 problems which they think
important, but they don't know what to do. Now, let me warn you about important
problems. The importance is not the consequences.
All the time I was at Bell Labs, no one worked on the three outstanding
problems in physics. Time travel,
teleportation and anti gravity.
They're not important because you haven't gotten attack.
The importance of a problem to a great extent depends upon.
Have you got a way of attacking the problem?
Problems are not important per se, although they have some consequences.
The most important thing that makes a problem important is
that there is an attack. You have an idea how I can go about that
problem. You want to watch it just
because the economic consequences are great. And take those three of them.
Anti gravity, teleportation, or time travel. The economic consequences
are unbelievably large, but they're not
important problems. You have an idea how to do it. When you have,
then they may become important.
Now, quite a few times, I would practice saying the following. It is not
what you do, it's the way that you do it.
It's the style you go about doing things. It's inverting the problem or changing it.
In the words of the song. It ain't what you do, it's the way that
you do it. It's the style of which you do it
that makes the difference. You only look
at special relativity. Poincare had it
all. Several other people had it all before, but Einstein did it the right
way. And you only remember Einstein as having done special relativity.
The other guys had it all. They even gave talks on it,
but they had it screwed up the subject. They didn't have it really clear and
straightforward. Now, when you first do a thing, it's often muddled up.
And one of your problems is to get it clear so it can be communicated
to other people. And you can spend a lot of time lying in bed saying,
well, gee, how can I say that to Joe? If I try it this way,
Joe might misunderstand that. How about that? How about this?
Until you finally have a way of looking at a problem which looks simple,
straightforward and clear so you can communicate it to others. It may not
be the way you found it, it often is not.
But getting it clear is important. Which brings me to the topic of communication.
You need to learn to communicate orally in
talks like this, written and written reports and
casual conversations. In the middle of a conference, you have to be able to
get up and say, that's wrong. For these reasons, bing, bing, bing, bing.
And you win. If you sit around and say, well,
I'll write a report tomorrow after I've thought about it some more,
the Decision is made, we go ahead and it doesn't matter what you do then.
The ability to communicate at three levels. Now, how do you learn it? You can
read books if you want it, but forget it. The way you learn,
as far as I'm concerned, is every time you go to a talk, you listen
not only to the talk, but to the style that's done. What talks
are effective? Why were they effective? What aspects of the
speaker could you adapt? For example,
if you're going to give after dinner speeches, generally speaking, there are three
jokes. One at the beginning when you get up, one in the middle to keep
them awake, and one last, when the soul will remember something that you said.
Well, I had to learn jokes. I discovered that I
cannot tell shaggy dog stories. I can tell one liners
very well, but I couldn't. I had to adapt my joke telling to what I
could do. Those who told shaggy dog stories, very interesting,
but I simply cannot do them very well. You have to adapt what
you learn from other speakers to you. When you find a person who is very
effective doing something, can you do it?
Why not? Maybe you can't.
Then you have to do something else. But if you yourself will learn
to criticize other talks, then you will have a critical basis
to criticize your own. And then you'll be able to give good
talks if you can only what books say, instead of learning your
own style of creativity. It is going to work. So I
think that the best thing you can do is start as of tomorrow.
When you hear lectures and talks, ask yourself every time,
besides, what was the content? What was the style?
What part can I adapt of that technique?
Why was that speech effective? Why is that speech not effective?
And you can ask your friends to check that your opinions are somewhat the same
as theirs. And you may find sometimes they don't agree with you. What's effective talk?
It's a bit of a problem there.
Now it's a poor workman who blames his tools.
I've always adopted a philosophy. I will do the best I
can with what I got. Thus, this school has
got a great many faults.
The bureaucracy in Washington periodically does strange things.
Other things, the students have peculiar features.
They have to disappear now and then. Well,
you don't blame the system you do at each
course and each lecture the best you can, given the circumstances.
This course is suffering from the fact that it's being broadcast. So you've all been
intimidated and afraid to raise your hand and say, hamming, I think you're crazy.
What about such and such? The Fall of this course with
the television on is that you people have been too intimidated. Well, I'll do
the best I can. I knew I perfectly well. I couldn't get you to interact
very actively in a class, so I gave up on that one. Though I did
get you one class lecture.
Now, there's another thing you have to recognize. If you're
going to have progress, there has to be change.
Change does not mean progress, but progress requires change.
Most people and most institutions don't like change.
They resent it. And therefore,
in order to make progress, you have to sort of welcome change.
You have to embrace it in spite of the fact you don't like it.
Why? We've always been doing it this way. Perfectly all right. Now, why should I
ever change? You can adopt the model I did.
If the department has been doing this for 10 years the same way,
it's time you should change to find out how to do it some other way.
I know it's perfectly satisfactory. Forget it. There might be better methods.
You'll never find out if you stay in the same damn rut.
Needless to say, most departments at Bell Labs didn't like my motto.
But that was my motto all the time. If you've been doing the same
thing for a long while, why is there no other method of doing it better?
You will never find other methods if you don't try other things.
Some other ones will make them worse occasionally. But without
change, you will not have progress.
Now, when you're learning things, I told you, you need to put hooks on ideas
so they can be covered widely. That was the thing that John Tooke could do
and I couldn't for so long. He could dredge up almost any kind of
information. After he told me, I could see that what
he said was true. But I couldn't think of it first. So I
started doing what he did. When I got a new piece of information, I turned
it around many ways until, as it were, it was connected with many
pieces of information so that in various situations that would become available.
And it has worked out fairly well.
Now you're likely to say to yourself, you haven't got the freedom to work.
I didn't either. When I began, I had to do
more or less what was expected. When you hire a plumber to fix
the plumbing, you expect him to be already trained.
You expect to be able. You don't give
a person a big, lovely chance to do something great when they
already demonstrated greatness. The onus is on you
to demonstrate greatness, and then you will get the opportunities.
It's not the other way around. As beautifully put by an
instructor. When I was at Nebraska, the instructor went
to head department and said, I want to be relieved of some teaching so I
can do some research. The head department said,
when you've done the research, I'll relieve you of the teaching.
You have to demonstrate your ability first and then you'll have the freedom
to do it. Otherwise, no. I had to
do error correcting codes at home on my own time. After I became
more able, the management left me alone. In fact, at the back end, the management
clearly had the belief. The more we left Hamming alone, the more he'd worry
about what should be done, the more likely he's going to do the right thing.
That applied to a guy like Hamming who had a conscience and was
worried. It doesn't apply to some people. Some people, you give them freedom, they'll do
nothing. But I was compulsive and I was worried about doing the right job.
So I did.
Now I have to ask the question, is effort to be
a great person worth it? Now, great is by definition of what you
think is great. Not mine. Is it worth it?
I will claim yes. I've talked to various people now,
people who tried to succeed and didn't.
I was afraid to ask. But those who did succeed and were famous,
I asked them, was the struggle worth it? And they said, yep, it's better than
wine, women in a song put together. I didn't ask any
women. They might have said, better wine, men in song, I don't know. But they
all thought that doing something really first class and knowing you've done
it is better than anything else they could think of.
I can't give you a report of the guys who didn't do it. As I
said, I was afraid to ask them. I didn't want to embarrass them.
Well, let me come down now to a saying of Socrates,
who lived about 470 to 399 BC in
Greece. He said,
the unexamined life is not worth living.
I heard it when I was cross first time I heard it when I was
crossing the campus at Yale behind a professor and a student.
And the professor turned to the student again and said, the unexamined life is
not worth living. And before request the whole quad, he had said it
three times. The unexamined life is not worth living.
You should examine your life. You've only got one life to lead
as far as any of us know. Why shouldn't it be the life you
want to have, instead of whatever happens to you,
to come down the back and say, well, I didn't do any harm. I had
an enjoyable life. Is that what you want to say in your old age?
You just had a good time in life? Or do you want to say,
you know, I did something that was important, at least something that I thought was
important. That's your problem, therefore, to pick these things
up and do it if you want to have a happy life in the back
end.
Now, I think all these questions are style. I kept saying
several times, you've got to work on the right problem at the right time in
the right way, otherwise you're doomed. Style is everything,
and it's not communicable in words. I cannot tell you what
makes a great painting. I can show you once. I can show you success,
which I've done in this class. Now, in summary,
in a sense, I want to give you a different view of the whole course,
particularly this lecture. I'm a revivalist preacher.
If you want, I'm saying, repent your
idle ways and get down and be somebody worth
being. This is what this lecture is all about.
Revivalist preacher, preaching. Well, now I've told
you things how to succeed. No one ever
told me these things. I've been telling you nobody.
I had to find them for myself. I've told you how to succeed.
You have no excuse for not doing better than I did.
Thank you.