This lecture was originally delivered to graduate students at the Naval Postgraduate School in Monterrey, California, on June 6, 1995. The lecture was the last lecture of a capstone course taught by Dr. Richard Hamming called “The Art of Doing Science and Engineering.”
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.
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 “You and Your Career.” 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 do simple things, but the major decisions I was not really involved in. To put it bluntly, and unpleasantly, I was envious—plain envious. I began to ask, “what's the difference between the really capable scientists and myself?” I began to study their work. I went to Bell Labs and I studied further.
This is really a report on what I found to be the difference between the first class and the second class. I want to remind you of something which is not in the notes of something called “The Matthew Effect” named after Saint Matthew. There is a verse in the Bible which says,
Whoever has will be given more,
and they will have an abundance.
Whoever does not have,
even what they have will be taken from them.
Or to put it more bluntly: those with God gets, and those that haven't got…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 to IBM and so on. And when I went there they would show me this or that about what’s going on. They’d show me the research labs or production lines and so on. I got to know more information than the other person. Once famous it's very easy remain famous.
Once not famous, what you do do will be taken away from you. 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 important to talk to you. 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. I suggest you a live a life of doing something significant by your definition. Your definition of significant is what makes it 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. I am really trying to get you to think about doing significant things by your definition of significant.
I have to talk about my own experience, I have throughout the course because if I talk about other peoples’ experience, it doesn't have the effect. My premise is to stick a knife in your back and give it a good twist and make you say it back end. Both having to do it, and say, “why couldn't I? After all, he’s are not that much better than I am.” It’s doubtful he is better than you are. My purpose in telling direct stories is to make you conscious so 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 as 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 computing. I was brought in to help get him out, so he go back to physics. And I knew he'd get a Nobel Prize for something. He was one of the people. You’ve seen the energy and ability. He was going to do something. It was in the nature of him to be something.
Yes luck favored 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 few months I was there, Shannon, Miss 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 amount of people around. Yes, it was in the air, but why did we do it? Why was it us?
Shannon had done all the good things before then. 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 as famous for writing five papers in one year in a journal, several which are very great classics.
It is luck, and it isn't. It’s both. It is and it is not. You prepare yourself for the way you want to lead from day to day. You prepare yourself for success or you don't. When the lightning strikes you are 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 he would have done other significant things. He'd done a bunch before he would do ones afterwards. I sort of deny it’s all luck.
Sir Isaac Newton observed that if other people thought as hard as he did, they would get the same results. 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, they went on hiking in the mountains behind Los Alamos. They still talk shop. They were at the problem all the time.
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 his biographies. He really didn't look unusual to anybody until after he came up to Cambridge in college. His mathematical knowledge was about arithmetic when he came. He's an exception and a few others.
Einstein after he got his doctor's degree he had no legitimate job, except for seven years in the Patent Office. No job in a university. He didn't get early recognition. When he got it, he did it. 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. Plenty other people didn't. A personal example (he's dead now so I can tell you) a guy named Bill Fan walked to my office at Bell Labs. He wanted to do Zone Melting. With zone melting you have a bar, and you have a coil round it which you heat by abduction to melt the metal. 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 the other side. Many, many passes removed the impurities from the middle of bar.
He had some equations. I put some algebra on it and some calculus and got some partial answers but I can see that he needed computing. I went around to his department and asked about him. They didn't think much of them. I go back to my office. I thought he had a good idea. I had resolved to work with important people. I wanted to do important work, and 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.
I reflected, Mohammed had to leave town, flee for his life. A prophet is not honored 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. He picked up all kinds of prizes. He became a famous man. His laboratory was made a national treasure. 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 with Zone Melting was his one great idea, but it was what Bell Labs needed. We needed to be able to make uranium without very many impurities. Then we needed to be able to put as many as we wanted 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. You make a thousand passes or something 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 important.
Now having disposed of psychological objections of luck and lack of high IQ because some of you say, “well I was the brightest student in our class,” so what. It doesn't matter. Let's get down to other things.
The most important thing about 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. You can’t be too overconfident, but you should have a fair amount of confidence.
Take for example Shannon. You remember when I did the 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'll tell you another story. For about a year, he came in about ten o'clock, played chess till about 2:00, and went home. At the end of year, the company gave him a salary raise. That's all you could see he was doing, but at home he was creating information theory. The way he played chess, is the following…
When you get 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, and more complex. Finally he would stop and think for a long while, grab his Queen, and say, “I ain’t scared nuttin’. Bing. The whole game would collapse then because he finally precipitated all pending operations and either won or lost. I learned that expression, “I ain't scared of nothing.” I've used this several times on myself, when I was stuck and I didn't know what on earth to do. I said good for Shannon, it’s good enough for Hamming. I ain’t scared of nothing, let's go ahead and see what happens.” Sometimes by copying his style I came through to success. I deliberately copied his style.
Another example, I hope most people are dead, I guess they aren’t but they probably won’t hear this. I was in a math department and we used to go to lunch together. They played games, threw boomerangs, flew kites, and played this and that and they’d fiddle around. I want to succeed, and I said to myself, “I can't afford to waste lunch time,” so I went around to the physics table where I'd written a paper with one the physicists and asked if I could join them.
Sure, I'm welcome to. The table consists among other people of Bardeen Shockley and Bratton, nobel prize winners, JB Johnson and some others. My friend Louis and I choose 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. Finally the Nobel Prize came through, promotion came through, jobs elsewhere came through, and all the able people left, including my friend. He promoted up line well. What was left was the dregs, hardly worthy eating lunch with.
Over in another corner of the dining room was a big table chemists and I had written a paper on nuclear Baghdad residence with one of the guys, so I asked if they minded if I joined them. I sit and we talk about chemistry and such other things for a long while. 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 Bell Labs my friend chemists stopped me and said, “you know Hemming, that remark of yours got underneath my skin. I've spent the summer thinking about the important problems 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 know he is a member 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 liking important why are you doing it” the one man who could, did become important. He did 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 can't work on all them the time because that's what Nobel Prize winners do. They get a Nobel Prize and then they think, like Shannon, they can also they can only work on important problems, and 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 to do small things. The great thing wrong with Nobel Prizes is you now think you only work on important problems. You don't. 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, when you get famous, you get put on all kinds of committees and other things. You can't get any work done. They stop you from doing it by various promotions That’s a lot of the reason why Nobel Prize winners often don't do very much afterwards.
Confidence is important. Over-confidence is of course is a disaster. I'll put as I did the other day—the difference between being strong-willed and stubborn. There is a fine line. I’ve seen a lot of people abandon a good idea too soon. I've seen people cling to a bad idea too long. They're both difficult problems.
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. 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. That will give you some unity. 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 staggered less and gets the distance proportional to n.
When you have a vision, you will go a long way. Without a vision, what you're going to do 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. An 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 do a first-class job.”
What you may consider good working relations may not be for you it's very sad but what do you think are good working relations are not. The example I've given you already is working with the door closed door open. If you work with the 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 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. I cannot prove to you whether the open door causes the open mind or whether the open mind causes the open door. I can only establish the correlation and it was quite spectacular. Almost always the guys with the door closed were often very well able, very gifted but they seemed to work always on slightly the wrong problem.
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 in Princeton. They take in people who've done something great, they give them the luxury of a beautiful office, a beautiful restaurant to dine in, wonderful grounds and everything else. They have 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 them continue working on the problem they made that made them famous. They keep on elaborating on that. They've already made it famous. It doesn’t need to be added to. They got the thing going. Rarely do they change.
von Neumann was different. He was at the Institute and he did go out in reality. He turned up in Washington and in other places. He traveled widely and was receptive of new ideas. But the bulk of the people got to a point the Institute for Advanced Study don't keep the door open on life as it were. 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 you think are the ideal working conditions, are not.
I'll give you some examples of this.
When we began with the IBM 701 computer, we programmed in absolute binary. There were a bunch of these machines at West Coast airframe companies and the rest were scattered around. It became obvious to me that the width the West Coast used for programming. Namely we’d hire an acre of girls, spread out, and they program. Typically girls, in those days. What was clear to me Bell Labs would never give me an acre of girls. They weren't about doing that kind of a thing.
What do I do? I am in computing, I want to be in the frontier. What everybody else has, I'm not going to have. I could quit, get a job on the west coast. Probably anyone airframes companies could use me 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 about trying to learn how to be great, so I’m studying great people.) So I think for a long while one day I said to myself, “Hamming you believe a machine can do anything. Why don't you make the machine do the programming?”
What was 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 us of all the stories a similar way what appears to be a defect is an asset. 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 into great success.
Another example is slightly different. When I was doing this 28-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 analogue machine at that time could do it because they didn't have the required accuracy.
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. One day I realized I was going to have to fill in a report of what I did because government contracts always require reports. 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 a problem. I was really demonstrating something much more important.
I promptly started deriving a better method of integrating the differential equations. I finally use method which for some years was known as Hammings method. I don't recommend it now but it was very suitable for the machines as they were.
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, this report has a very jazzy method of solving differential equation. Instead of a very crummy method. Both are equally effective, but one was defensible and one was not. I changed the nature of 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 the Hamming method if I had not realized that the method I was using which was adequate for me and we were all going to see if we're getting right answer, but it was not nice. It was not clean and as simple. It was rather ugly. So I changed the problem.
…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. 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 to 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.
One day I found John Tukey with whom I working extensively was my age and the guy was clearly a genius. I went in to our mutual boss and says, “Hendrick how can anybody my age know so much as John Tukey does?” He leaned back in his chair grinned at me and said, “Hamming you'd be surprised how much you know if you worked as hard as he did.” I slunk out the office, there wasn't anything to say.
When I was home I thought, “Frankly I am not working really as hard as I could. I'll ever 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 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 very deliberately as a book review editor. There's always a book on my coffee table waiting to be read and reviewed. When a review is written by me, I set aside for about a week and ask myself afterwards, is that a good review? Does that really digest the book? If it doesn't, you're rereading the book or writing a better review.
This way I forced myself to get a lot wide acquaintance in computer science. 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. My wife complained occasionally that all I looked in at the New Yorker were 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.
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 ripe what problem is ripe and how to go about it the right problem at the right time the right way where it counts and nothing else counts. Nothing. It's easy there's a million races being run you just got to get in one time and win.
I met you earlier in regard to the chemists about one of 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 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 is 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 of 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 of it can linger around the Saturday and Sunday. If you do it Monday morning there's a hot conference at 10 o'clock and bingo, everything's broken up. I use Friday afternoon for many many years. I recommend 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.
I've regularly tried to 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 understand what is relevant to my field, and what is interesting but is not relevant.
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. 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 a theory is true you won't. 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. They'll make you just a good one, which I'm not complaining about but greatness consists of seeing what other people have missed, seizing the contradictions and making the new step forward. You have to tolerate ambiguity.
I have not the faintest idea how I'll ever teach a course in ambiguity. I've thought about many times. how will I put a course together to teach students to tolerate ambiguity? I haven't a clue. I don't know what to do. I really tell you that the tolerance of ambiguity, not being so certain everything is correct is a necessary feature.
Most great scientists have 10 to 20 problems in their minds, which when they get a clue how to attack, they drop other things and bless you that problem finish it off first. Something between 10 and 20 problems which they think import but you don't know what to do. Let me warn you about important problems. Importance is not the consequences. All the hours 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 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 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 until you have an idea how to do it. When you have an attack then they may become important.
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 a style you go about doing things. It's inverting the problem. It’s the style of what you do that makes the difference.
Look at special relativity. Others had said it all before. But Einstein said it the right way. You only remember Einstein having done special relativity. The other guys had it all. They even gave talks on it but they had it screwed up. They didn't have it really clear and straightforward.
When you first do a thing it is often muddled up. One of your problems is to get it clear so it can be communicated to other people. You've 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 never misunderstand?” how about that? how about this? until you finally have a way of looking the problem which looks simple and straightforward and clear, so you can communicate it to others. It may not be the way you found it. Often is not. 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 communicate on 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, if you're going to give after-dinner speeches generally speaking there are three jokes: one the beginning when you get up, one the middle to keep awake, and one last one solo to remember something that you said. I had to learn jokes. I discovered that I cannot tell shaggy dog stories. I can tell one liners very well, but I had to adapt my joke-telling to what I could do. Those who told shaggy dog stories were very interesting, by I simply cannot do it 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 learn something else. If you learn to criticize other talks then you will have a critical basis to correctly criticize your own and then you'll be able to give your talks. if you can only follow what books say this versus learning your own style of creativity it isn’t going to work. 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 a Content what was the style? what part can I adapt that technique? why is that speech effective? why is that a 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 on what's effective.
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 like 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 is being broadcast. So you all might have been intimidated to raise your hands 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 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.
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.
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 weapons. you'll never find out who you stay in the same damn rut. needless to say most apartments Bell Labs didn't like my model but that was my model 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.
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. I got new piece of information. I turned it around many ways until is it were it was connected with many pieces of information so that in various situations that idea would come available, and it has worked out fairly well. You're likely to saying to yourself, “you haven’t got the freedom to work.” I didn’t either when I began. I had to do more with less respect.
When you hire a plumber to fix the plumbing you expect them do you already trained. You expect them 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. Beautifully put by an instructor when I was at Nebraska. The instructor went to the head of the Department said I want to be relieved as some teaching so I do some research. The Department head 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, management left me alone. In fact the management clearly had to believe 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 him freedom they'll do nothing. But I was compulsive and I was worried about doing a great job so I did.
I have to ask the question, “is effort to be a great person worth it?” Now great is by the definition of what you think is great, not mine. Is it worth it. I will claim yes. I've talked to various people who tried to succeed and didn't. I was afraid to ask but those who didn't succeed and were famous I asked, was the struggle worth it and they said yep “it's better than wine women and song put together” I didn't ask any women. They might have said it was better 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 about 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 for us to turn the student again said “the unexamined life is not worth living.” and before we crossed the whole quad he incited 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 end 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 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.
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 once I can show you success which I've done this class.
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 revivals 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.
Still Interested? Check my Hamming compendium.