Hamming, "You and Your Research" (June 6, 1995)

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.