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 read 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 persons .. people who keep
the thing going but whose opinion is not matter a great deal. They could trust me 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. I began to ask myself: 'what's the difference between the really capable
scientists, and myself?' And, I studied it — I went up to Bell Labs I studied it further. This
is really a report on what I found differently 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
Saint Matthew. There is a verse there in the Bible which says 'unto those who have shall it be given;
unto who have not shall it be taken away.' Or to put a bluntly 'those with got gets,
and those what 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 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 Saint Matthew said. Now, why do I believe it's an important
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 in 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's
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 'Well, if Hamming can do it, why couldn't I?' After all, he's not that
much better than I am. It's doubtful he is better than you are. So, my purpose in telling direct
stories is to make you conscious but you can be at least as great or better than I was, and I didn't
do badly. Now, I'll start psychological rather logically. The first objection people have is:
'well, fame is a matter of luck.' I have cited regularly Pasteur's remark 'Luck favors the
prepared mind.' Yes, there is an element of luck; no, there isn't. for example when I met Feynman
he was running in computing, I was brought in to help get him out, so he 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 favors the 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 time 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 the 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 which are very great classics. It isn't luck; it is, too — I gotta say both it is and it
is not. You prepare yourself the way you lead from day to day, will 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 if
Shannon had not created information theory 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 its 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.' 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 we went on 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 — consider 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 a university. He didn't get early recognition. But when he got it,
he did it. And that indicates that the IQs or such other things which people are supposed to have,
it's a help 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. A good many other people didn't. A
personal example, he's dead now so I can tell you, a guy named Bill Pfann walked to my office at Bell
Labs, and he want to do zone melting. Now, zone melting, you have a bar, you have a coil around
it which you heat by induction to melt the metal, and you move it down slowly. If the impurities
stay in solution, you drag the impurities down. If impurities trying to drop out, they're
pushed to the other side. And many many passes remove the impurities from the middle of bar.
Well, he has some equations. I put some algebra on it and some calculus - got some partial answers,
but I can 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: Mohammed 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 -- zone 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 and we needed to be able to put as many Watts 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 a thousand
passes or something, that's why you can't do it numerically other than with a computing machine,
because a thousand passes will have end effects and they bounce around. So I was right that time.
I guessed the man has something important, and 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 class), So what? Doesn't
matter. Let's get down to other things. Now, the most important thing probably in great people is
they believe they can do great work. They have confidence in themselves. If you don't think
you do good 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 point 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'll tell you another wave, simply. There was a year so when he came in about ten o'clock,
played chess 'til about 2:00 and went home. At the end of the year, the company gave him
a salary raise. That's all you could see him doing was that, but at home he was creating
information theory. Well the way he played chess is the following: when you are attacked in chess,
you could either defend yourself or you attack back. Shannon never defended himself. He attacked
back. And the game would get tied up more more more more complex and finally he's stop and
think for a long while, grab his Queen, advance, and say 'I ain't scared of nuttin!' Bingo -- the
whole game would collapse then, because he finally precipitated all pending operations and either won
or lost. Well I learned that expression 'I ain't scared of nothing.' I've used this several times
on myself. When stuck and I didn't know what on earth to do, I said: good enough for Shannon,
good enough for Hamming, I ain't scared of 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 of the people are dead, but unless they aren't, 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, threw boomerangs, flew kites, and played this and that, and they fiddled around. And
I want to succeed, as I can't afford to waste lunch times. So I went around to the physics
table where I'd written a paper with one of the physicists (a good one) and I said 'may I join
you?' Sure, I'm welcome. The table consists, among other people, of Bardeen, Shockley, and Brattain
(the Nobel prize winners), JB Johnson (Johnson noise), and some others, my friend Ron Louis.
And I used to have lunch with them 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, sensible. Well
finally the Nobel Prize came through, promotion came through, jobs elsewhere came through, and all
the able people left, including my friend. He was promoted up the line. Well what was left was the
dregs. Hardly worth eating lunch with. But over in another corner in 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: you mind if I join you? So I sit down and we talk about chemistry and such other
things for a long while, and finally one day I walk in to 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 of 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 ten or twelve years ago, I notice he is a member of the National Academy
of Engineering. I have never heard of anything about any other person at that chemistry table.
Not one. The one man who could hear — 'if what you were doing is not important, not likely important,
why are you doing it?' — the one man who could, did become important. He did succeed. The
rest of 'em 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 or -- now, you can't work on all the time because that's what Nobel Prize
winners do. They get a Nobel Prize and then 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 mighty oak trees. But you have to plant the acorns which will grow. You have to
learn the small things. So the great thing, 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 a problem which
can become important and matter, which have a future, which will grow into mighty oak trees.
Another thing that ruins Nobel Prize winners, of course, is everybody gets
famous, you're put into all kinds of committees, all kinds of other things,
and you can't get any work done. They stop you from doing it. By various promotions to 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 as I did the other day: the difference between being strong-willed and
stubborn. The difference of being 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 do regularly is a desire to do excellent work. Whatever you do, you're going to do well.
Now it's not true, as 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 can just sign them, you don't try and write your handwriting, your most beautiful one you
can. You just get rid of it. But, in general, you try and do excellence. This 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 staggered a couple steps this way
and a couple this way and a couple this way. In a total of many many steps he gets the distance
to 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 or 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 a first-class job.
Now what you may consider good working relations may not be for you. It's very sad but what do you
think are good working conditions are not. The example I've given you already is working with
the door closed or open. If you work the door closed, you won't be interrupted and you get
your work done. You work 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 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 have 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 whether the open mind causes the
open door. I suspect it -- 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 seem
to work always on slightly the wrong problem. So you'll have to get wide feeling for what is going
on and the supreme example of this closure is the Institute for Advanced Study at Princeton. They
take in people who've done something great. They give them luxury, a beautiful office a beautiful
restaurant to dine in, a wonderful grounds and everything else like that. Adequate salary to
live on. No cares, no worries, no nothing, you're freed for life on anything at all. What happens?
The bulk of 'em continue working on the problem they made 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 the
Institute and he did go out in reality and turn up in Washington in other places. He traveled
widely and was receptive of new ideas. But the bulk of the people got appointed the 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 had done before. They are very able people, but the Institute in my opinion
sterilized them a great extent. So what do you think are the ideal working conditions are 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 at a West Coast airframe companies and
the rest were scattered around. Now it became obvious to me that the methods 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. Shat was clear to me: Bell
Labs would never give me an acre of girls. They weren't about doing that kind of a thing. Well
what do I do? I want to be 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 a number of airframe companies, 'cus I was reasonably well-known 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 out trying to learn how to be great so I'm studying
great people. Bell Lab's a place to study. But the Airframe's a place were to get a tool. So I think
for a long while one day I said 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 for us? What appeared to be a defect, by turning the problem around, became an asset.
Grace Hopper has told several other stories 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 net wherewithal to
do it, if you turn the problem around you can turn it into great success. Another one is slightly
different. When I was doing this 20th order system equation (I told you about the 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 of that day could do it because they didn't have the required
accuracy. Well I was using a variation of Mill's method which was pretty crummy — I'd had found
Mills method was unstable, had patched up a little bit, there it was. One day,
I realized the following: I was going to have to fill in a report of what I did because government
contracts always require reports and everybody who had analog computer was going to try and
pick flaws and what I did because I was really showing that a digital machine could beat the
analog on his own home ground. That's really what I was doing, not getting the answer to a 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 use method which is 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. This report has a very jazzy method of solving differential equations instead of a
very crummy method. Both are 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 originally was get the answers
of 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's method if I had not realized that
the method I were using which was adequate for me and we go all see we're getting right answer
but it was not nice was not clean and simple, it was rather ugly, so I changed the problem.
Now these are all tell you issues 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 a second story changing the nature 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
not only from 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 this 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
do study other people, how they succeed, 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've told you a story before although I'll repeat it, one day I found John
Tukey with whom I working extensively, was my age and the guy was clearly a genius, I went
in my our mutual boss and says Hendrick how can anybody my age know so much as John Tukey 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 the office, there wasn't anything to say,
and I stayed home. When I was home I thought: frankly, 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 in reading nonsense magazines and thumbing through newspaper. 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, there's always a book on my coffee
table right next to it, waiting to be read and review written. When a review is written by me,
I set aside a week and ask myself afterwards 'is that a good review?' Does that read, I guess,
the book. If it doesn't, you're rereading the book and writing a better review. This way I
forced myself to get a lot wide acquaintance in computer science and being a 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 like what rue godmother thing. My wife would complain
occasionally that all I looked in the 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 other
things and did that. It's not hard to do, you just do it. Now I want to say another couple 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 can try and teach you something about style and taste,
so you'll be able to have some hunch of when the problem is right, what problem is right,
and how to go about it. The right problem at the right time the right way -- it 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 'em 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 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&T? What should I be doing
in computing? What is the nature of software? My friends all after a while got to know:
Friday afternoons, great thoughts. What's the nature of this that the other thing? I spent 10
percent of my time trying to answer the question what are the important problems in my field? 10
percent. Friday afternoon, straight through. Don't do it Monday morning because you'll be interrupted
immediately. If you do it Friday afternoon some thoughts can linger around to Saturday and Sunday.
You do it Monday morning, there's a hot conference at 10 o'clock and bingo everything's broken up. I
use it Friday afternoon for many many years, I recommend it. 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'll
have some idea of where you're headed, so you can march in a uniform direction and get far,
rather being a drunken sailor and getting nowhere. And I've regular to this picture
tried to stress this lecture stress the bigger picture. I've tried to stress fundamentals. No
one knows what the fundamentals will be tomorrow, but you can 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 a 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 do.
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 that 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 a theory is true, you won't. But they disbelieved 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,
it consists of seeing what other people have missed and seizing behind 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 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 merely tell you that 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,
ones you just hanging around, which when they get a clue how to attack, they drop other things
and rush to that problem, finish it off first. Something between 10 and 20 problems which they
think import but they don't know what to do. Now let me warn you about important problems:
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 got an 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 portent 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 until you have an idea how to do it. When you have, then they may become important.
Now I've been quite a few times I would practically 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 in which you do it. It makes the difference. You only look at special relativity,
Poincaré had it all, several other people had it all before, but Einstein did it the right way,
and you only remember Einstein of having done special relativity. The other guys had it all,
they even gave talks on it, but they had it screwed up to some degree. They didn't have
it really clear and straightforward. Now when you first do a thing, its often muddled up, and one
of your problems is to get it clear so it can be communicated to other people. And you can spent a
lot of time lying in bed saying well gee how can I say that to Joe. If I try it this way, Jill might
have misunderstand that. How about that? How about this? Until you finally have a way of looking the
problem which looks simple straightforward and clear, so you can communicate it to others. It
may not be the way you found, 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 reports, and casual conversations. In the middle of a conference, you have to be able to
go up to say 'that's wrong for these reasons, Bing Bing Bing Bing.' And you win if you sit around and
say well all right report tomorrow after I've thought about some more, the decision is made,
we go ahead, and it doesn't matter what you do then. The ability communicated three levels. How
do you learn it? You can read books if you want to, 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 talk but to the style that's
done. What talks are effective? Why were they effective? What aspects of the speaker can you
adapt? For example, in your if you're going to give after-dinner speeches, generally speaking,
there are three jokes: one near the beginning when you get up, one in the middle to keep awake,
and one last one so they'll 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, they're very
interesting, but I simply cannot do them very well. You have to adapt what you learn for other
speakers to you. When you find a person was very effective doing something, can you do it? Why not?
Maybe you can't. Then you have to something else. But if you the self will learn to criticize other
talks then you will have a critical basis to correct criticize your own and then you'll be
able to give your talks. If you can only follow what books say, without learning your own style
of creativity, it isn't going to work. So I think that the best thing you could 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 in that technique? Why is that speech effective? Why was
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 trapped
adopted philosophy I will do the best I can with what I got. Thus this school has got a great many
faults: 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 has
suffered from the fact it is being broadcast, so you 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 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 the 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 the fact you don't like it. Why with all of you do you say it perfectly alright now
why should I be change, you can adopt the motto 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 were doing for 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 of the 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 recover widely. That was the thing that John Tukey 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 the what he said was true, but I couldn't think of it first. So I started
doing what he did: where I got new piece of information, I turned it around many ways until,
as it were, it was connected with many piece of information so that in various situations
that would come 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 neither when I began. I had to do more or less
what you'd expect. When you hire a plumber to fix the plumbing, you expect them to be already
trained. You expect to be able. You don't give a person or big lovely chance to do something great
when they have not already demonstrated greatness. The onus is on you to demonstrate greatness,
and then you'll get the opportunities. It's not the other way around. As beautifully put by a
instructor when I was at Nebraska, the instructor went ahead to the department said I want to be
relieved of some teaching so I do some research. The head of the Department said: when you've done
the research, I'll relieve you of the teaching. You 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, manager left me alone, in fact the backend management
clearly had the belief 'the more we left Hamming alone, the more he'd worry about what should
be done, more like 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 him freedom,
they'll do nothing. But I was compulsive and I was really 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 I said 'yep, it's better than wine,
women, and song put together.' I didn't ask any women, they might have said better than 'wine men,
and 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. I didn't want to embarrass
them. Well let me come down now to a saying of Socrates who lived off 470 to 399 BC and Greece,
he said the unexamined life is not worth living. I heard it while I was crossed first time I heard
while crossing the campus at Yale behind a professor and a student. Professor turned to
the student again and said the unexamined life is not worth living, and before he'd crossed
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 should it be
the life you want to happen, instead of whatever happens to you. To come down the bag and say well
I didn't do any harm, I had an enjoyable life, is that what you want to say 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 is not communicable in words. I
cannot tell you what makes a great painting. I can show you ones. I can show you success,
which I've done this class. Now to summarize, 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 it for
myself. I've told you how to succeed. You have no excuse for not doing better than I did. Thank you.