The Economy

I wrote a post a couple of weeks ago in which I said macroeconomic collapse “may happen” and a few friends asked me why.  To be clear, I don’t think it’s the likely outcome—I think we’ll find a way to address our challenges.  But here is what some of the challenges are.

Most of these issues would be not so bad by themselves; the problem is that we have all of them in aggregate.

1)   US GDP growth in real dollars is low (and trending down).  It was -2.9% for Q1 2014 after the second official revision [1].  If it’s down again for Q2, we’ll be in a recession.

(I wrote about this in more detail here.)

2)   Government debt is high.  In fact, it’s quietly crossed over 100% of GDP for the first time since post-World War II.  Debt like this is maybe ok if the economy is growing fast, but ours is not.  And given demographic headwinds, etc., debt levels are likely to face further challenges.  Here is a graph of our government debt to GDP. [2]

3)   Government spending is high. Here are graphs of total government spending and federal spending as a share of GDP. [3] Total government spending has risen from about 8% of GDP to above 40% of GDP.  Spending on social support programs has grown the fastest.  Defense spending has been on a reasonable decline since WWII.  Personally, I think that current levels of social support spending are ok (though maybe the spending should be distributed differently), and we should probably do more.  But I think we need to plan for it.  In addition to thinking about new sorts of jobs to replace lost jobs that aren’t coming back, we should probably think about things like some version of a basic income.  I'm not sure it's the optimal solution (in fact, I have a strong intuitive bias against it) but I can't come up with a better suggestion, and I think it would probably lead to less waste than current social safety net systems.


4)   Interest rates are low—in fact, we’ve been near zero for 5 years, and on a steady trajectory down for 30.  This is historically highly unusual.   In fact, with quantitative easing, rates are really less than zero (and they are officially negative in Europe).  On the positive side, but as you’d expect with near-zero rates, US equities are at record levels.

5)   Personal savings rates are low.

On the other hand, corporate savings rates are high.  US corporations hold 2.3x as much cash as they held 20 years ago, after adjusting for inflation.  Individuals aren’t saving as much, and companies aren’t investing as much.

As I said at the beginning, all of this interrelates.  Any one data point could be fine in isolation, but if, for example, interest rates are zero (or government spending is high), you’d like to see growth be high because people should be borrowing money and investing it.

I think that startups and venture capital will continue to do well.  Most investors don’t want to hold cash, for obvious reasons, and so they’re looking for high-growth places to invest.  But I’m a little unsure how much the startup world and the rest of the economy can decouple.

To reiterate, I think we’ll find a way through these economic challenges.  But I think it’s important we not ignore it and pretend it will magically get better, which seems to be the current plan.  Personally, I think that innovation and new technology is what will save us.

We need to get back to natural economic growth.  The US has been very fortunate to have a long history of growth—we had roughly 100 years of territory expansion and then roughly 100 years of incredible technological innovation.  I think the path from our troubles will involve finding a way for economic growth to continue.





You and Your Research, by Richard Hamming

Richard Hamming gave this talk in March of 1986. [1]  It's one of the best talks I've ever read and has long impacted how I think about spending my time.

I mentioned it to a number of people this weekend who, to my surprise, had never heard of it.  So I though I'd share it here:

[Addition 5/28/23: see this great annotated version from Gwern.]

It's a pleasure to be here. I doubt if I can live up to the Introduction. The title of my talk is, ``You and Your Research.'' It is not about managing research, it is about how you individually do your research. I could give a talk on the other subject - but it's not, it's about you. I'm not talking about ordinary run-of-the-mill research; I'm talking about great research. And for the sake of describing great research I'll occasionally say Nobel-Prize type of work. It doesn't have to gain the Nobel Prize, but I mean those kinds of things which we perceive are significant things. Relativity, if you want, Shannon's information theory, any number of outstanding theories - that's the kind of thing I'm talking about.

Now, how did I come to do this study? At Los Alamos I was brought in to run the computing machines which other people had got going, so those scientists and physicists could get back to business. I saw I was a stooge. I saw that although physically I was the same, they were different. And to put the thing bluntly, I was envious. I wanted to know why they were so different from me. I saw Feynman up close. I saw Fermi and Teller. I saw Oppenheimer. I saw Hans Bethe: he was my boss. I saw quite a few very capable people. I became very interested in the difference between those who do and those who might have done.

When I came to Bell Labs, I came into a very productive department. Bode was the department head at the time; Shannon was there, and there were other people. I continued examining the questions, ``Why?'' and ``What is the difference?'' I continued subsequently by reading biographies, autobiographies, asking people questions such as: ``How did you come to do this?'' I tried to find out what are the differences. And that's what this talk is about.

Now, why is this talk important? I think it is important because, as far as I know, each of you has one life to live. Even if you believe in reincarnation it doesn't do you any good from one life to the next! Why shouldn't you do significant things in this one life, however you define significant? I'm not going to define it - you know what I mean. I will talk mainly about science because that is what I have studied. But so far as I know, and I've been told by others, much of what I say applies to many fields. Outstanding work is characterized very much the same way in most fields, but I will confine myself to science.

In order to get at you individually, I must talk in the first person. I have to get you to drop modesty and say to yourself, ``Yes, I would like to do first-class work.'' Our society frowns on people who set out to do really good work. You're not supposed to; luck is supposed to descend on you and you do great things by chance. Well, that's a kind of dumb thing to say. I say, why shouldn't you set out to do something significant. You don't have to tell other people, but shouldn't you say to yourself, ``Yes, I would like to do something significant.''

In order to get to the second stage, I have to drop modesty and talk in the first person about what I've seen, what I've done, and what I've heard. I'm going to talk about people, some of whom you know, and I trust that when we leave, you won't quote me as saying some of the things I said.

Let me start not logically, but psychologically. I find that the major objection is that people think great science is done by luck. It's all a matter of luck. Well, consider Einstein. Note how many different things he did that were good. Was it all luck? Wasn't it a little too repetitive? Consider Shannon. He didn't do just information theory. Several years before, he did some other good things and some which are still locked up in the security of cryptography. He did many good things.

You see again and again, that it is more than one thing from a good person. Once in a while a person does only one thing in his whole life, and we'll talk about that later, but a lot of times there is repetition. I claim that luck will not cover everything. And I will cite Pasteur who said, ``Luck favors the prepared mind.'' And I think that says it the way I believe it. There is indeed an element of luck, and no, there isn't. The prepared mind sooner or later finds something important and does it. So yes, it is luck. The particular thing you do is luck, but that you do something is not.

For example, when I came to Bell Labs, I shared an office for a while with Shannon. At the same time he was doing information theory, I was doing coding theory. It is suspicious that the two of us did it at the same place and at the same time - it was in the atmosphere. And you can say, ``Yes, it was luck.'' On the other hand you can say, ``But why of all the people in Bell Labs then were those the two who did it?'' Yes, it is partly luck, and partly it is the prepared mind; but `partly' is the other thing I'm going to talk about. So, although I'll come back several more times to luck, I want to dispose of this matter of luck as being the sole criterion whether you do great work or not. I claim you have some, but not total, control over it. And I will quote, finally, Newton on the matter. Newton said, ``If others would think as hard as I did, then they would get similar results.''

One of the characteristics you see, and many people have it including great scientists, is that usually when they were young they had independent thoughts and had the courage to pursue them. For example, Einstein, somewhere around 12 or 14, asked himself the question, ``What would a light wave look like if I went with the velocity of light to look at it?'' Now he knew that electromagnetic theory says you cannot have a stationary local maximum. But if he moved along with the velocity of light, he would see a local maximum. He could see a contradiction at the age of 12, 14, or somewhere around there, that everything was not right and that the velocity of light had something peculiar. Is it luck that he finally created special relativity? Early on, he had laid down some of the pieces by thinking of the fragments. Now that's the necessary but not sufficient condition. All of these items I will talk about are both luck and not luck.

How about having lots of `brains?' It sounds good. Most of you in this room probably have more than enough brains to do first-class work. But great work is something else than mere brains. Brains are measured in various ways. In mathematics, theoretical physics, astrophysics, typically brains correlates to a great extent with the ability to manipulate symbols. And so the typical IQ test is apt to score them fairly high. On the other hand, in other fields it is something different. For example, Bill Pfann, the fellow who did zone melting, came into my office one day. He had this idea dimly in his mind about what he wanted and he had some equations. It was pretty clear to me that this man didn't know much mathematics and he wasn't really articulate. His problem seemed interesting so I took it home and did a little work. I finally showed him how to run computers so he could compute his own answers. I gave him the power to compute. He went ahead, with negligible recognition from his own department, but ultimately he has collected all the prizes in the field. Once he got well started, his shyness, his awkwardness, his inarticulateness, fell away and he became much more productive in many other ways. Certainly he became much more articulate.

And I can cite another person in the same way. I trust he isn't in the audience, i.e. a fellow named Clogston. I met him when I was working on a problem with John Pierce's group and I didn't think he had much. I asked my friends who had been with him at school, ``Was he like that in graduate school?'' ``Yes,'' they replied. Well I would have fired the fellow, but J. R. Pierce was smart and kept him on. Clogston finally did the Clogston cable. After that there was a steady stream of good ideas. One success brought him confidence and courage.

One of the characteristics of successful scientists is having courage. Once you get your courage up and believe that you can do important problems, then you can. If you think you can't, almost surely you are not going to. Courage is one of the things that Shannon had supremely. You have only to think of his major theorem. He wants to create a method of coding, but he doesn't know what to do so he makes a random code. Then he is stuck. And then he asks the impossible question, ``What would the average random code do?'' He then proves that the average code is arbitrarily good, and that therefore there must be at least one good code. Who but a man of infinite courage could have dared to think those thoughts? That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.

Age is another factor which the physicists particularly worry about. They always are saying that you have got to do it when you are young or you will never do it. Einstein did things very early, and all the quantum mechanic fellows were disgustingly young when they did their best work. Most mathematicians, theoretical physicists, and astrophysicists do what we consider their best work when they are young. It is not that they don't do good work in their old age but what we value most is often what they did early. On the other hand, in music, politics and literature, often what we consider their best work was done late. I don't know how whatever field you are in fits this scale, but age has some effect.

But let me say why age seems to have the effect it does. In the first place if you do some good work you will find yourself on all kinds of committees and unable to do any more work. You may find yourself as I saw Brattain when he got a Nobel Prize. The day the prize was announced we all assembled in Arnold Auditorium; all three winners got up and made speeches. The third one, Brattain, practically with tears in his eyes, said, ``I know about this Nobel-Prize effect and I am not going to let it affect me; I am going to remain good old Walter Brattain.'' Well I said to myself, ``That is nice.'' But in a few weeks I saw it was affecting him. Now he could only work on great problems.

When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn't the way things go. So that is another reason why you find that when you get early recognition it seems to sterilize you. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren't good afterwards, but they were superb before they got there and were only good afterwards.

This brings up the subject, out of order perhaps, of working conditions. What most people think are the best working conditions, are not. Very clearly they are not because people are often most productive when working conditions are bad. One of the better times of the Cambridge Physical Laboratories was when they had practically shacks - they did some of the best physics ever.

I give you a story from my own private life. Early on it became evident to me that Bell Laboratories was not going to give me the conventional acre of programming people to program computing machines in absolute binary. It was clear they weren't going to. But that was the way everybody did it. I could go to the West Coast and get a job with the airplane companies without any trouble, but the exciting people were at Bell Labs and the fellows out there in the airplane companies were not. I thought for a long while about, ``Did I want to go or not?'' and I wondered how I could get the best of two possible worlds. I finally said to myself, ``Hamming, you think the machines can do practically everything. Why can't you make them write programs?'' What appeared at first to me as a defect forced me into automatic programming very early. What appears to be a fault, often, by a change of viewpoint, turns out to be one of the greatest assets you can have. But you are not likely to think that when you first look the thing and say, ``Gee, I'm never going to get enough programmers, so how can I ever do any great programming?''

And there are many other stories of the same kind; Grace Hopper has similar ones. I think that if you look carefully you will see that often the great scientists, by turning the problem around a bit, changed a defect to an asset. For example, many scientists when they found they couldn't do a problem finally began to study why not. They then turned it around the other way and said, ``But of course, this is what it is'' and got an important result. So ideal working conditions are very strange. The ones you want aren't always the best ones for you.

Now for the matter of drive. You observe that most great scientists have tremendous drive. I worked for ten years with John Tukey at Bell Labs. He had tremendous drive. One day about three or four years after I joined, I discovered that John Tukey was slightly younger than I was. John was a genius and I clearly was not. Well I went storming into Bode's office and said, ``How can anybody my age know as much as John Tukey does?'' He leaned back in his chair, put his hands behind his head, grinned slightly, and said, ``You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.'' I simply slunk out of the office!

What Bode was saying was this: ``Knowledge and productivity are like compound interest.'' Given two people of approximately the same ability and one person who works ten percent more than the other, the latter will more than twice outproduce the former. The more you know, the more you learn; the more you learn, the more you can do; the more you can do, the more the opportunity - it is very much like compound interest. I don't want to give you a rate, but it is a very high rate. Given two people with exactly the same ability, the one person who manages day in and day out to get in one more hour of thinking will be tremendously more productive over a lifetime. I took Bode's remark to heart; I spent a good deal more of my time for some years trying to work a bit harder and I found, in fact, I could get more work done. I don't like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done. There's no question about this.

On this matter of drive Edison says, ``Genius is 99% perspiration and 1% inspiration.'' He may have been exaggerating, but the idea is that solid work, steadily applied, gets you surprisingly far. The steady application of effort with a little bit more work, intelligently applied is what does it. That's the trouble; drive, misapplied, doesn't get you anywhere. I've often wondered why so many of my good friends at Bell Labs who worked as hard or harder than I did, didn't have so much to show for it. The misapplication of effort is a very serious matter. Just hard work is not enough - it must be applied sensibly.

There's another trait on the side which I want to talk about; that trait is ambiguity. It took me a while to discover its importance. Most people like to believe something is or is not true. Great scientists tolerate ambiguity very well. They believe the theory enough to go ahead; they doubt it enough to notice the errors and faults so they can step forward and create the new replacement theory. If you believe too much you'll never notice the flaws; if you doubt too much you won't get started. It requires a lovely balance. But most great scientists are well aware of why their theories are true and they are also well aware of some slight misfits which don't quite fit and they don't forget it. Darwin writes in his autobiography that he found it necessary to write down every piece of evidence which appeared to contradict his beliefs because otherwise they would disappear from his mind. When you find apparent flaws you've got to be sensitive and keep track of those things, and keep an eye out for how they can be explained or how the theory can be changed to fit them. Those are often the great contributions. Great contributions are rarely done by adding another decimal place. It comes down to an emotional commitment. Most great scientists are completely committed to their problem. Those who don't become committed seldom produce outstanding, first-class work.

Now again, emotional commitment is not enough. It is a necessary condition apparently. And I think I can tell you the reason why. Everybody who has studied creativity is driven finally to saying, ``creativity comes out of your subconscious.'' Somehow, suddenly, there it is. It just appears. Well, we know very little about the subconscious; but one thing you are pretty well aware of is that your dreams also come out of your subconscious. And you're aware your dreams are, to a fair extent, a reworking of the experiences of the day. If you are deeply immersed and committed to a topic, day after day after day, your subconscious has nothing to do but work on your problem. And so you wake up one morning, or on some afternoon, and there's the answer. For those who don't get committed to their current problem, the subconscious goofs off on other things and doesn't produce the big result. So the way to manage yourself is that when you have a real important problem you don't let anything else get the center of your attention - you keep your thoughts on the problem. Keep your subconscious starved so it has to work on your problem, so you can sleep peacefully and get the answer in the morning, free.

Now Alan Chynoweth mentioned that I used to eat at the physics table. I had been eating with the mathematicians and I found out that I already knew a fair amount of mathematics; in fact, I wasn't learning much. The physics table was, as he said, an exciting place, but I think he exaggerated on how much I contributed. It was very interesting to listen to Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay and other people, and I was learning a lot. But unfortunately a Nobel Prize came, and a promotion came, and what was left was the dregs. Nobody wanted what was left. Well, there was no use eating with them!

Over on the other side of the dining hall was a chemistry table. I had worked with one of the fellows, Dave McCall; furthermore he was courting our secretary at the time. I went over and said, ``Do you mind if I join you?'' They can't say no, so I started eating with them for a while. And I started asking, ``What are the important problems of your field?'' And after a week or so, ``What important problems are you working on?'' And after some more time I came in one day and said, ``If what you are doing is not important, and if you don't think it is going to lead to something important, why are you at Bell Labs working on it?'' I wasn't welcomed after that; I had to find somebody else to eat with! That was in the spring.

In the fall, Dave McCall stopped me in the hall and said, ``Hamming, that remark of yours got underneath my skin. I thought about it all summer, i.e. what were the important problems in my field. I haven't changed my research,'' he says, ``but I think it was well worthwhile.'' And I said, ``Thank you Dave,'' and went on. I noticed a couple of months later he was made the head of the department. I noticed the other day he was a Member of the National Academy of Engineering. I noticed he has succeeded. I have never heard the names of any of the other fellows at that table mentioned in science and scientific circles. They were unable to ask themselves, ``What are the important problems in my field?''

If you do not work on an important problem, it's unlikely you'll do important work. It's perfectly obvious. Great scientists have thought through, in a careful way, a number of important problems in their field, and they keep an eye on wondering how to attack them. Let me warn you, `important problem' must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn't work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. When I say that most scientists don't work on important problems, I mean it in that sense. The average scientist, so far as I can make out, spends almost all his time working on problems which he believes will not be important and he also doesn't believe that they will lead to important problems.

I spoke earlier about planting acorns so that oaks will grow. You can't always know exactly where to be, but you can keep active in places where something might happen. And even if you believe that great science is a matter of luck, you can stand on a mountain top where lightning strikes; you don't have to hide in the valley where you're safe. But the average scientist does routine safe work almost all the time and so he (or she) doesn't produce much. It's that simple. If you want to do great work, you clearly must work on important problems, and you should have an idea.

Along those lines at some urging from John Tukey and others, I finally adopted what I called ``Great Thoughts Time.'' When I went to lunch Friday noon, I would only discuss great thoughts after that. By great thoughts I mean ones like: ``What will be the role of computers in all of AT&T?'', ``How will computers change science?'' For example, I came up with the observation at that time that nine out of ten experiments were done in the lab and one in ten on the computer. I made a remark to the vice presidents one time, that it would be reversed, i.e. nine out of ten experiments would be done on the computer and one in ten in the lab. They knew I was a crazy mathematician and had no sense of reality. I knew they were wrong and they've been proved wrong while I have been proved right. They built laboratories when they didn't need them. I saw that computers were transforming science because I spent a lot of time asking ``What will be the impact of computers on science and how can I change it?'' I asked myself, ``How is it going to change Bell Labs?'' I remarked one time, in the same address, that more than one-half of the people at Bell Labs will be interacting closely with computing machines before I leave. Well, you all have terminals now. I thought hard about where was my field going, where were the opportunities, and what were the important things to do. Let me go there so there is a chance I can do important things.

Most great scientists know many important problems. They have something between 10 and 20 important problems for which they are looking for an attack. And when they see a new idea come up, one hears them say ``Well that bears on this problem.'' They drop all the other things and get after it. Now I can tell you a horror story that was told to me but I can't vouch for the truth of it. I was sitting in an airport talking to a friend of mine from Los Alamos about how it was lucky that the fission experiment occurred over in Europe when it did because that got us working on the atomic bomb here in the US. He said ``No; at Berkeley we had gathered a bunch of data; we didn't get around to reducing it because we were building some more equipment, but if we had reduced that data we would have found fission.'' They had it in their hands and they didn't pursue it. They came in second!

The great scientists, when an opportunity opens up, get after it and they pursue it. They drop all other things. They get rid of other things and they get after an idea because they had already thought the thing through. Their minds are prepared; they see the opportunity and they go after it. Now of course lots of times it doesn't work out, but you don't have to hit many of them to do some great science. It's kind of easy. One of the chief tricks is to live a long time!

Another trait, it took me a while to notice. I noticed the following facts about people who work with the door open or the door closed. I notice that if you have the door to your office closed, you get more work done today and tomorrow, and you are more productive than most. But 10 years later somehow you don't know quite know what problems are worth working on; all the hard work you do is sort of tangential in importance. He who works with the door open gets all kinds of interruptions, but he also occasionally gets clues as to what the world is and what might be important. Now I cannot prove the cause and effect sequence because you might say, ``The closed door is symbolic of a closed mind.'' I don't know. But I can say there is a pretty good correlation between those who work with the doors open and those who ultimately do important things, although people who work with doors closed often work harder. Somehow they seem to work on slightly the wrong thing - not much, but enough that they miss fame.

I want to talk on another topic. It is based on the song which I think many of you know, ``It ain't what you do, it's the way that you do it.'' I'll start with an example of my own. I was conned into doing on a digital computer, in the absolute binary days, a problem which the best analog computers couldn't do. And I was getting an answer. When I thought carefully and said to myself, ``You know, Hamming, you're going to have to file a report on this military job; after you spend a lot of money you're going to have to account for it and every analog installation is going to want the report to see if they can't find flaws in it.'' I was doing the required integration by a rather crummy method, to say the least, but I was getting the answer. And I realized that in truth the problem was not just to get the answer; it was to demonstrate for the first time, and beyond question, that I could beat the analog computer on its own ground with a digital machine. I reworked the method of solution, created a theory which was nice and elegant, and changed the way we computed the answer; the results were no different. The published report had an elegant method which was later known for years as ``Hamming's Method of Integrating Differential Equations.'' It is somewhat obsolete now, but for a while it was a very good method. By changing the problem slightly, I did important work rather than trivial work.

In the same way, when using the machine up in the attic in the early days, I was solving one problem after another after another; a fair number were successful and there were a few failures. I went home one Friday after finishing a problem, and curiously enough I wasn't happy; I was depressed. I could see life being a long sequence of one problem after another after another. After quite a while of thinking I decided, ``No, I should be in the mass production of a variable product. I should be concerned with all of next year's problems, not just the one in front of my face.'' By changing the question I still got the same kind of results or better, but I changed things and did important work. I attacked the major problem - How do I conquer machines and do all of next year's problems when I don't know what they are going to be? How do I prepare for it? How do I do this one so I'll be on top of it? How do I obey Newton's rule? He said, ``If I have seen further than others, it is because I've stood on the shoulders of giants.'' These days we stand on each other's feet!

You should do your job in such a fashion that others can build on top of it, so they will indeed say, ``Yes, I've stood on so and so's shoulders and I saw further.'' The essence of science is cumulative. By changing a problem slightly you can often do great work rather than merely good work. Instead of attacking isolated problems, I made the resolution that I would never again solve an isolated problem except as characteristic of a class.

Now if you are much of a mathematician you know that the effort to generalize often means that the solution is simple. Often by stopping and saying, ``This is the problem he wants but this is characteristic of so and so. Yes, I can attack the whole class with a far superior method than the particular one because I was earlier embedded in needless detail.'' The business of abstraction frequently makes things simple. Furthermore, I filed away the methods and prepared for the future problems.

To end this part, I'll remind you, ``It is a poor workman who blames his tools - the good man gets on with the job, given what he's got, and gets the best answer he can.'' And I suggest that by altering the problem, by looking at the thing differently, you can make a great deal of difference in your final productivity because you can either do it in such a fashion that people can indeed build on what you've done, or you can do it in such a fashion that the next person has to essentially duplicate again what you've done. It isn't just a matter of the job, it's the way you write the report, the way you write the paper, the whole attitude. It's just as easy to do a broad, general job as one very special case. And it's much more satisfying and rewarding!

I have now come down to a topic which is very distasteful; it is not sufficient to do a job, you have to sell it. `Selling' to a scientist is an awkward thing to do. It's very ugly; you shouldn't have to do it. The world is supposed to be waiting, and when you do something great, they should rush out and welcome it. But the fact is everyone is busy with their own work. You must present it so well that they will set aside what they are doing, look at what you've done, read it, and come back and say, ``Yes, that was good.'' I suggest that when you open a journal, as you turn the pages, you ask why you read some articles and not others. You had better write your report so when it is published in the Physical Review, or wherever else you want it, as the readers are turning the pages they won't just turn your pages but they will stop and read yours. If they don't stop and read it, you won't get credit.

There are three things you have to do in selling. You have to learn to write clearly and well so that people will read it, you must learn to give reasonably formal talks, and you also must learn to give informal talks. We had a lot of so-called `back room scientists.' In a conference, they would keep quiet. Three weeks later after a decision was made they filed a report saying why you should do so and so. Well, it was too late. They would not stand up right in the middle of a hot conference, in the middle of activity, and say, ``We should do this for these reasons.'' You need to master that form of communication as well as prepared speeches.

When I first started, I got practically physically ill while giving a speech, and I was very, very nervous. I realized I either had to learn to give speeches smoothly or I would essentially partially cripple my whole career. The first time IBM asked me to give a speech in New York one evening, I decided I was going to give a really good speech, a speech that was wanted, not a technical one but a broad one, and at the end if they liked it, I'd quietly say, ``Any time you want one I'll come in and give you one.'' As a result, I got a great deal of practice giving speeches to a limited audience and I got over being afraid. Furthermore, I could also then study what methods were effective and what were ineffective.

While going to meetings I had already been studying why some papers are remembered and most are not. The technical person wants to give a highly limited technical talk. Most of the time the audience wants a broad general talk and wants much more survey and background than the speaker is willing to give. As a result, many talks are ineffective. The speaker names a topic and suddenly plunges into the details he's solved. Few people in the audience may follow. You should paint a general picture to say why it's important, and then slowly give a sketch of what was done. Then a larger number of people will say, ``Yes, Joe has done that,'' or ``Mary has done that; I really see where it is; yes, Mary really gave a good talk; I understand what Mary has done.'' The tendency is to give a highly restricted, safe talk; this is usually ineffective. Furthermore, many talks are filled with far too much information. So I say this idea of selling is obvious.

Let me summarize. You've got to work on important problems. I deny that it is all luck, but I admit there is a fair element of luck. I subscribe to Pasteur's ``Luck favors the prepared mind.'' I favor heavily what I did. Friday afternoons for years - great thoughts only - means that I committed 10% of my time trying to understand the bigger problems in the field, i.e. what was and what was not important. I found in the early days I had believed `this' and yet had spent all week marching in `that' direction. It was kind of foolish. If I really believe the action is over there, why do I march in this direction? I either had to change my goal or change what I did. So I changed something I did and I marched in the direction I thought was important. It's that easy.

Now you might tell me you haven't got control over what you have to work on. Well, when you first begin, you may not. But once you're moderately successful, there are more people asking for results than you can deliver and you have some power of choice, but not completely. I'll tell you a story about that, and it bears on the subject of educating your boss. I had a boss named Schelkunoff; he was, and still is, a very good friend of mine. Some military person came to me and demanded some answers by Friday. Well, I had already dedicated my computing resources to reducing data on the fly for a group of scientists; I was knee deep in short, small, important problems. This military person wanted me to solve his problem by the end of the day on Friday. I said, ``No, I'll give it to you Monday. I can work on it over the weekend. I'm not going to do it now.'' He goes down to my boss, Schelkunoff, and Schelkunoff says, ``You must run this for him; he's got to have it by Friday.'' I tell him, ``Why do I?''; he says, ``You have to.'' I said, ``Fine, Sergei, but you're sitting in your office Friday afternoon catching the late bus home to watch as this fellow walks out that door.'' I gave the military person the answers late Friday afternoon. I then went to Schelkunoff's office and sat down; as the man goes out I say, ``You see Schelkunoff, this fellow has nothing under his arm; but I gave him the answers.'' On Monday morning Schelkunoff called him up and said, ``Did you come in to work over the weekend?'' I could hear, as it were, a pause as the fellow ran through his mind of what was going to happen; but he knew he would have had to sign in, and he'd better not say he had when he hadn't, so he said he hadn't. Ever after that Schelkunoff said, ``You set your deadlines; you can change them.''

One lesson was sufficient to educate my boss as to why I didn't want to do big jobs that displaced exploratory research and why I was justified in not doing crash jobs which absorb all the research computing facilities. I wanted instead to use the facilities to compute a large number of small problems. Again, in the early days, I was limited in computing capacity and it was clear, in my area, that a ``mathematician had no use for machines.'' But I needed more machine capacity. Every time I had to tell some scientist in some other area, ``No I can't; I haven't the machine capacity,'' he complained. I said ``Go tell your Vice President that Hamming needs more computing capacity.'' After a while I could see what was happening up there at the top; many people said to my Vice President, ``Your man needs more computing capacity.'' I got it!

I also did a second thing. When I loaned what little programming power we had to help in the early days of computing, I said, ``We are not getting the recognition for our programmers that they deserve. When you publish a paper you will thank that programmer or you aren't getting any more help from me. That programmer is going to be thanked by name; she's worked hard.'' I waited a couple of years. I then went through a year of BSTJ articles and counted what fraction thanked some programmer. I took it into the boss and said, ``That's the central role computing is playing in Bell Labs; if the BSTJ is important, that's how important computing is.'' He had to give in. You can educate your bosses. It's a hard job. In this talk I'm only viewing from the bottom up; I'm not viewing from the top down. But I am telling you how you can get what you want in spite of top management. You have to sell your ideas there also.

Well I now come down to the topic, ``Is the effort to be a great scientist worth it?'' To answer this, you must ask people. When you get beyond their modesty, most people will say, ``Yes, doing really first-class work, and knowing it, is as good as wine, women and song put together,'' or if it's a woman she says, ``It is as good as wine, men and song put together.'' And if you look at the bosses, they tend to come back or ask for reports, trying to participate in those moments of discovery. They're always in the way. So evidently those who have done it, want to do it again. But it is a limited survey. I have never dared to go out and ask those who didn't do great work how they felt about the matter. It's a biased sample, but I still think it is worth the struggle. I think it is very definitely worth the struggle to try and do first-class work because the truth is, the value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends, in my opinion.

I've told you how to do it. It is so easy, so why do so many people, with all their talents, fail? For example, my opinion, to this day, is that there are in the mathematics department at Bell Labs quite a few people far more able and far better endowed than I, but they didn't produce as much. Some of them did produce more than I did; Shannon produced more than I did, and some others produced a lot, but I was highly productive against a lot of other fellows who were better equipped. Why is it so? What happened to them? Why do so many of the people who have great promise, fail?

Well, one of the reasons is drive and commitment. The people who do great work with less ability but who are committed to it, get more done that those who have great skill and dabble in it, who work during the day and go home and do other things and come back and work the next day. They don't have the deep commitment that is apparently necessary for really first-class work. They turn out lots of good work, but we were talking, remember, about first-class work. There is a difference. Good people, very talented people, almost always turn out good work. We're talking about the outstanding work, the type of work that gets the Nobel Prize and gets recognition.

The second thing is, I think, the problem of personality defects. Now I'll cite a fellow whom I met out in Irvine. He had been the head of a computing center and he was temporarily on assignment as a special assistant to the president of the university. It was obvious he had a job with a great future. He took me into his office one time and showed me his method of getting letters done and how he took care of his correspondence. He pointed out how inefficient the secretary was. He kept all his letters stacked around there; he knew where everything was. And he would, on his word processor, get the letter out. He was bragging how marvelous it was and how he could get so much more work done without the secretary's interference. Well, behind his back, I talked to the secretary. The secretary said, ``Of course I can't help him; I don't get his mail. He won't give me the stuff to log in; I don't know where he puts it on the floor. Of course I can't help him.'' So I went to him and said, ``Look, if you adopt the present method and do what you can do single-handedly, you can go just that far and no farther than you can do single-handedly. If you will learn to work with the system, you can go as far as the system will support you.'' And, he never went any further. He had his personality defect of wanting total control and was not willing to recognize that you need the support of the system.

You find this happening again and again; good scientists will fight the system rather than learn to work with the system and take advantage of all the system has to offer. It has a lot, if you learn how to use it. It takes patience, but you can learn how to use the system pretty well, and you can learn how to get around it. After all, if you want a decision `No', you just go to your boss and get a `No' easy. If you want to do something, don't ask, do it. Present him with an accomplished fact. Don't give him a chance to tell you `No'. But if you want a `No', it's easy to get a `No'.

Another personality defect is ego assertion and I'll speak in this case of my own experience. I came from Los Alamos and in the early days I was using a machine in New York at 590 Madison Avenue where we merely rented time. I was still dressing in western clothes, big slash pockets, a bolo and all those things. I vaguely noticed that I was not getting as good service as other people. So I set out to measure. You came in and you waited for your turn; I felt I was not getting a fair deal. I said to myself, ``Why? No Vice President at IBM said, `Give Hamming a bad time'. It is the secretaries at the bottom who are doing this. When a slot appears, they'll rush to find someone to slip in, but they go out and find somebody else. Now, why? I haven't mistreated them.'' Answer, I wasn't dressing the way they felt somebody in that situation should. It came down to just that - I wasn't dressing properly. I had to make the decision - was I going to assert my ego and dress the way I wanted to and have it steadily drain my effort from my professional life, or was I going to appear to conform better? I decided I would make an effort to appear to conform properly. The moment I did, I got much better service. And now, as an old colorful character, I get better service than other people.

You should dress according to the expectations of the audience spoken to. If I am going to give an address at the MIT computer center, I dress with a bolo and an old corduroy jacket or something else. I know enough not to let my clothes, my appearance, my manners get in the way of what I care about. An enormous number of scientists feel they must assert their ego and do their thing their way. They have got to be able to do this, that, or the other thing, and they pay a steady price.

John Tukey almost always dressed very casually. He would go into an important office and it would take a long time before the other fellow realized that this is a first-class man and he had better listen. For a long time John has had to overcome this kind of hostility. It's wasted effort! I didn't say you should conform; I said ``The appearance of conforming gets you a long way.'' If you chose to assert your ego in any number of ways, ``I am going to do it my way,'' you pay a small steady price throughout the whole of your professional career. And this, over a whole lifetime, adds up to an enormous amount of needless trouble.

By taking the trouble to tell jokes to the secretaries and being a little friendly, I got superb secretarial help. For instance, one time for some idiot reason all the reproducing services at Murray Hill were tied up. Don't ask me how, but they were. I wanted something done. My secretary called up somebody at Holmdel, hopped the company car, made the hour-long trip down and got it reproduced, and then came back. It was a payoff for the times I had made an effort to cheer her up, tell her jokes and be friendly; it was that little extra work that later paid off for me. By realizing you have to use the system and studying how to get the system to do your work, you learn how to adapt the system to your desires. Or you can fight it steadily, as a small undeclared war, for the whole of your life.

And I think John Tukey paid a terrible price needlessly. He was a genius anyhow, but I think it would have been far better, and far simpler, had he been willing to conform a little bit instead of ego asserting. He is going to dress the way he wants all of the time. It applies not only to dress but to a thousand other things; people will continue to fight the system. Not that you shouldn't occasionally!

When they moved the library from the middle of Murray Hill to the far end, a friend of mine put in a request for a bicycle. Well, the organization was not dumb. They waited awhile and sent back a map of the grounds saying, ``Will you please indicate on this map what paths you are going to take so we can get an insurance policy covering you.'' A few more weeks went by. They then asked, ``Where are you going to store the bicycle and how will it be locked so we can do so and so.'' He finally realized that of course he was going to be red-taped to death so he gave in. He rose to be the President of Bell Laboratories.

Barney Oliver was a good man. He wrote a letter one time to the IEEE. At that time the official shelf space at Bell Labs was so much and the height of the IEEE Proceedings at that time was larger; and since you couldn't change the size of the official shelf space he wrote this letter to the IEEE Publication person saying, ``Since so many IEEE members were at Bell Labs and since the official space was so high the journal size should be changed.'' He sent it for his boss's signature. Back came a carbon with his signature, but he still doesn't know whether the original was sent or not. I am not saying you shouldn't make gestures of reform. I am saying that my study of able people is that they don't get themselves committed to that kind of warfare. They play it a little bit and drop it and get on with their work.

Many a second-rate fellow gets caught up in some little twitting of the system, and carries it through to warfare. He expends his energy in a foolish project. Now you are going to tell me that somebody has to change the system. I agree; somebody's has to. Which do you want to be? The person who changes the system or the person who does first-class science? Which person is it that you want to be? Be clear, when you fight the system and struggle with it, what you are doing, how far to go out of amusement, and how much to waste your effort fighting the system. My advice is to let somebody else do it and you get on with becoming a first-class scientist. Very few of you have the ability to both reform the system and become a first-class scientist.

On the other hand, we can't always give in. There are times when a certain amount of rebellion is sensible. I have observed almost all scientists enjoy a certain amount of twitting the system for the sheer love of it. What it comes down to basically is that you cannot be original in one area without having originality in others. Originality is being different. You can't be an original scientist without having some other original characteristics. But many a scientist has let his quirks in other places make him pay a far higher price than is necessary for the ego satisfaction he or she gets. I'm not against all ego assertion; I'm against some.

Another fault is anger. Often a scientist becomes angry, and this is no way to handle things. Amusement, yes, anger, no. Anger is misdirected. You should follow and cooperate rather than struggle against the system all the time.

Another thing you should look for is the positive side of things instead of the negative. I have already given you several examples, and there are many, many more; how, given the situation, by changing the way I looked at it, I converted what was apparently a defect to an asset. I'll give you another example. I am an egotistical person; there is no doubt about it. I knew that most people who took a sabbatical to write a book, didn't finish it on time. So before I left, I told all my friends that when I come back, that book was going to be done! Yes, I would have it done - I'd have been ashamed to come back without it! I used my ego to make myself behave the way I wanted to. I bragged about something so I'd have to perform. I found out many times, like a cornered rat in a real trap, I was surprisingly capable. I have found that it paid to say, ``Oh yes, I'll get the answer for you Tuesday,'' not having any idea how to do it. By Sunday night I was really hard thinking on how I was going to deliver by Tuesday. I often put my pride on the line and sometimes I failed, but as I said, like a cornered rat I'm surprised how often I did a good job. I think you need to learn to use yourself. I think you need to know how to convert a situation from one view to another which would increase the chance of success.

Now self-delusion in humans is very, very common. There are enumerable ways of you changing a thing and kidding yourself and making it look some other way. When you ask, ``Why didn't you do such and such,'' the person has a thousand alibis. If you look at the history of science, usually these days there are 10 people right there ready, and we pay off for the person who is there first. The other nine fellows say, ``Well, I had the idea but I didn't do it and so on and so on.'' There are so many alibis. Why weren't you first? Why didn't you do it right? Don't try an alibi. Don't try and kid yourself. You can tell other people all the alibis you want. I don't mind. But to yourself try to be honest.

If you really want to be a first-class scientist you need to know yourself, your weaknesses, your strengths, and your bad faults, like my egotism. How can you convert a fault to an asset? How can you convert a situation where you haven't got enough manpower to move into a direction when that's exactly what you need to do? I say again that I have seen, as I studied the history, the successful scientist changed the viewpoint and what was a defect became an asset.

In summary, I claim that some of the reasons why so many people who have greatness within their grasp don't succeed are: they don't work on important problems, they don't become emotionally involved, they don't try and change what is difficult to some other situation which is easily done but is still important, and they keep giving themselves alibis why they don't. They keep saying that it is a matter of luck. I've told you how easy it is; furthermore I've told you how to reform. Therefore, go forth and become great scientists!


A. G. Chynoweth: Well that was 50 minutes of concentrated wisdom and observations accumulated over a fantastic career; I lost track of all the observations that were striking home. Some of them are very very timely. One was the plea for more computer capacity; I was hearing nothing but that this morning from several people, over and over again. So that was right on the mark today even though here we are 20 - 30 years after when you were making similar remarks, Dick. I can think of all sorts of lessons that all of us can draw from your talk. And for one, as I walk around the halls in the future I hope I won't see as many closed doors in Bellcore. That was one observation I thought was very intriguing.

Thank you very, very much indeed Dick; that was a wonderful recollection. I'll now open it up for questions. I'm sure there are many people who would like to take up on some of the points that Dick was making.

Hamming: First let me respond to Alan Chynoweth about computing. I had computing in research and for 10 years I kept telling my management, ``Get that !&@#% machine out of research. We are being forced to run problems all the time. We can't do research because were too busy operating and running the computing machines.'' Finally the message got through. They were going to move computing out of research to someplace else. I was persona non grata to say the least and I was surprised that people didn't kick my shins because everybody was having their toy taken away from them. I went in to Ed David's office and said, ``Look Ed, you've got to give your researchers a machine. If you give them a great big machine, we'll be back in the same trouble we were before, so busy keeping it going we can't think. Give them the smallest machine you can because they are very able people. They will learn how to do things on a small machine instead of mass computing.'' As far as I'm concerned, that's how UNIX arose. We gave them a moderately small machine and they decided to make it do great things. They had to come up with a system to do it on. It is called UNIX!

A. G. Chynoweth: I just have to pick up on that one. In our present environment, Dick, while we wrestle with some of the red tape attributed to, or required by, the regulators, there is one quote that one exasperated AVP came up with and I've used it over and over again. He growled that, ``UNIX was never a deliverable!''

Question: What about personal stress? Does that seem to make a difference?

Hamming: Yes, it does. If you don't get emotionally involved, it doesn't. I had incipient ulcers most of the years that I was at Bell Labs. I have since gone off to the Naval Postgraduate School and laid back somewhat, and now my health is much better. But if you want to be a great scientist you're going to have to put up with stress. You can lead a nice life; you can be a nice guy or you can be a great scientist. But nice guys end last, is what Leo Durocher said. If you want to lead a nice happy life with a lot of recreation and everything else, you'll lead a nice life.

Question: The remarks about having courage, no one could argue with; but those of us who have gray hairs or who are well established don't have to worry too much. But what I sense among the young people these days is a real concern over the risk taking in a highly competitive environment. Do you have any words of wisdom on this?

Hamming: I'll quote Ed David more. Ed David was concerned about the general loss of nerve in our society. It does seem to me that we've gone through various periods. Coming out of the war, coming out of Los Alamos where we built the bomb, coming out of building the radars and so on, there came into the mathematics department, and the research area, a group of people with a lot of guts. They've just seen things done; they've just won a war which was fantastic. We had reasons for having courage and therefore we did a great deal. I can't arrange that situation to do it again. I cannot blame the present generation for not having it, but I agree with what you say; I just cannot attach blame to it. It doesn't seem to me they have the desire for greatness; they lack the courage to do it. But we had, because we were in a favorable circumstance to have it; we just came through a tremendously successful war. In the war we were looking very, very bad for a long while; it was a very desperate struggle as you well know. And our success, I think, gave us courage and self confidence; that's why you see, beginning in the late forties through the fifties, a tremendous productivity at the labs which was stimulated from the earlier times. Because many of us were earlier forced to learn other things - we were forced to learn the things we didn't want to learn, we were forced to have an open door - and then we could exploit those things we learned. It is true, and I can't do anything about it; I cannot blame the present generation either. It's just a fact.

Question: Is there something management could or should do?

Hamming: Management can do very little. If you want to talk about managing research, that's a totally different talk. I'd take another hour doing that. This talk is about how the individual gets very successful research done in spite of anything the management does or in spite of any other opposition. And how do you do it? Just as I observe people doing it. It's just that simple and that hard!

Question: Is brainstorming a daily process?

Hamming: Once that was a very popular thing, but it seems not to have paid off. For myself I find it desirable to talk to other people; but a session of brainstorming is seldom worthwhile. I do go in to strictly talk to somebody and say, ``Look, I think there has to be something here. Here's what I think I see ...'' and then begin talking back and forth. But you want to pick capable people. To use another analogy, you know the idea called the `critical mass.' If you have enough stuff you have critical mass. There is also the idea I used to call `sound absorbers'. When you get too many sound absorbers, you give out an idea and they merely say, ``Yes, yes, yes.'' What you want to do is get that critical mass in action; ``Yes, that reminds me of so and so,'' or, ``Have you thought about that or this?'' When you talk to other people, you want to get rid of those sound absorbers who are nice people but merely say, ``Oh yes,'' and to find those who will stimulate you right back.

For example, you couldn't talk to John Pierce without being stimulated very quickly. There were a group of other people I used to talk with. For example there was Ed Gilbert; I used to go down to his office regularly and ask him questions and listen and come back stimulated. I picked my people carefully with whom I did or whom I didn't brainstorm because the sound absorbers are a curse. They are just nice guys; they fill the whole space and they contribute nothing except they absorb ideas and the new ideas just die away instead of echoing on. Yes, I find it necessary to talk to people. I think people with closed doors fail to do this so they fail to get their ideas sharpened, such as ``Did you ever notice something over here?'' I never knew anything about it - I can go over and look. Somebody points the way. On my visit here, I have already found several books that I must read when I get home. I talk to people and ask questions when I think they can answer me and give me clues that I do not know about. I go out and look!

Question: What kind of tradeoffs did you make in allocating your time for reading and writing and actually doing research?

Hamming: I believed, in my early days, that you should spend at least as much time in the polish and presentation as you did in the original research. Now at least 50% of the time must go for the presentation. It's a big, big number.

Question: How much effort should go into library work?

Hamming: It depends upon the field. I will say this about it. There was a fellow at Bell Labs, a very, very, smart guy. He was always in the library; he read everything. If you wanted references, you went to him and he gave you all kinds of references. But in the middle of forming these theories, I formed a proposition: there would be no effect named after him in the long run. He is now retired from Bell Labs and is an Adjunct Professor. He was very valuable; I'm not questioning that. He wrote some very good Physical Review articles; but there's no effect named after him because he read too much. If you read all the time what other people have done you will think the way they thought. If you want to think new thoughts that are different, then do what a lot of creative people do - get the problem reasonably clear and then refuse to look at any answers until you've thought the problem through carefully how you would do it, how you could slightly change the problem to be the correct one. So yes, you need to keep up. You need to keep up more to find out what the problems are than to read to find the solutions. The reading is necessary to know what is going on and what is possible. But reading to get the solutions does not seem to be the way to do great research. So I'll give you two answers. You read; but it is not the amount, it is the way you read that counts.

Question: How do you get your name attached to things?

Hamming: By doing great work. I'll tell you the hamming window one. I had given Tukey a hard time, quite a few times, and I got a phone call from him from Princeton to me at Murray Hill. I knew that he was writing up power spectra and he asked me if I would mind if he called a certain window a ``Hamming window.'' And I said to him, ``Come on, John; you know perfectly well I did only a small part of the work but you also did a lot.'' He said, ``Yes, Hamming, but you contributed a lot of small things; you're entitled to some credit.'' So he called it the hamming window. Now, let me go on. I had twitted John frequently about true greatness. I said true greatness is when your name is like ampere, watt, and fourier - when it's spelled with a lower case letter. That's how the hamming window came about.

Question: Dick, would you care to comment on the relative effectiveness between giving talks, writing papers, and writing books?

Hamming: In the short-haul, papers are very important if you want to stimulate someone tomorrow. If you want to get recognition long-haul, it seems to me writing books is more contribution because most of us need orientation. In this day of practically infinite knowledge, we need orientation to find our way. Let me tell you what infinite knowledge is. Since from the time of Newton to now, we have come close to doubling knowledge every 17 years, more or less. And we cope with that, essentially, by specialization. In the next 340 years at that rate, there will be 20 doublings, i.e. a million, and there will be a million fields of specialty for every one field now. It isn't going to happen. The present growth of knowledge will choke itself off until we get different tools. I believe that books which try to digest, coordinate, get rid of the duplication, get rid of the less fruitful methods and present the underlying ideas clearly of what we know now, will be the things the future generations will value. Public talks are necessary; private talks are necessary; written papers are necessary. But I am inclined to believe that, in the long-haul, books which leave out what's not essential are more important than books which tell you everything because you don't want to know everything. I don't want to know that much about penguins is the usual reply. You just want to know the essence.

Question: You mentioned the problem of the Nobel Prize and the subsequent notoriety of what was done to some of the careers. Isn't that kind of a much more broad problem of fame? What can one do?

Hamming: Some things you could do are the following. Somewhere around every seven years make a significant, if not complete, shift in your field. Thus, I shifted from numerical analysis, to hardware, to software, and so on, periodically, because you tend to use up your ideas. When you go to a new field, you have to start over as a baby. You are no longer the big mukity muk and you can start back there and you can start planting those acorns which will become the giant oaks. Shannon, I believe, ruined himself. In fact when he left Bell Labs, I said, ``That's the end of Shannon's scientific career.'' I received a lot of flak from my friends who said that Shannon was just as smart as ever. I said, ``Yes, he'll be just as smart, but that's the end of his scientific career,'' and I truly believe it was.

You have to change. You get tired after a while; you use up your originality in one field. You need to get something nearby. I'm not saying that you shift from music to theoretical physics to English literature; I mean within your field you should shift areas so that you don't go stale. You couldn't get away with forcing a change every seven years, but if you could, I would require a condition for doing research, being that you will change your field of research every seven years with a reasonable definition of what it means, or at the end of 10 years, management has the right to compel you to change. I would insist on a change because I'm serious. What happens to the old fellows is that they get a technique going; they keep on using it. They were marching in that direction which was right then, but the world changes. There's the new direction; but the old fellows are still marching in their former direction.

You need to get into a new field to get new viewpoints, and before you use up all the old ones. You can do something about this, but it takes effort and energy. It takes courage to say, ``Yes, I will give up my great reputation.'' For example, when error correcting codes were well launched, having these theories, I said, ``Hamming, you are going to quit reading papers in the field; you are going to ignore it completely; you are going to try and do something else other than coast on that.'' I deliberately refused to go on in that field. I wouldn't even read papers to try to force myself to have a chance to do something else. I managed myself, which is what I'm preaching in this whole talk. Knowing many of my own faults, I manage myself. I have a lot of faults, so I've got a lot of problems, i.e. a lot of possibilities of management.

Question: Would you compare research and management?

Hamming: If you want to be a great researcher, you won't make it being president of the company. If you want to be president of the company, that's another thing. I'm not against being president of the company. I just don't want to be. I think Ian Ross does a good job as President of Bell Labs. I'm not against it; but you have to be clear on what you want. Furthermore, when you're young, you may have picked wanting to be a great scientist, but as you live longer, you may change your mind. For instance, I went to my boss, Bode, one day and said, ``Why did you ever become department head? Why didn't you just be a good scientist?'' He said, ``Hamming, I had a vision of what mathematics should be in Bell Laboratories. And I saw if that vision was going to be realized, I had to make it happen; I had to be department head.'' When your vision of what you want to do is what you can do single-handedly, then you should pursue it. The day your vision, what you think needs to be done, is bigger than what you can do single-handedly, then you have to move toward management. And the bigger the vision is, the farther in management you have to go. If you have a vision of what the whole laboratory should be, or the whole Bell System, you have to get there to make it happen. You can't make it happen from the bottom very easily. It depends upon what goals and what desires you have. And as they change in life, you have to be prepared to change. I chose to avoid management because I preferred to do what I could do single-handedly. But that's the choice that I made, and it is biased. Each person is entitled to their choice. Keep an open mind. But when you do choose a path, for heaven's sake be aware of what you have done and the choice you have made. Don't try to do both sides.

Question: How important is one's own expectation or how important is it to be in a group or surrounded by people who expect great work from you?

Hamming: At Bell Labs everyone expected good work from me - it was a big help. Everybody expects you to do a good job, so you do, if you've got pride. I think it's very valuable to have first-class people around. I sought out the best people. The moment that physics table lost the best people, I left. The moment I saw that the same was true of the chemistry table, I left. I tried to go with people who had great ability so I could learn from them and who would expect great results out of me. By deliberately managing myself, I think I did much better than laissez faire.

Question: You, at the outset of your talk, minimized or played down luck; but you seemed also to gloss over the circumstances that got you to Los Alamos, that got you to Chicago, that got you to Bell Laboratories.

Hamming: There was some luck. On the other hand I don't know the alternate branches. Until you can say that the other branches would not have been equally or more successful, I can't say. Is it luck the particular thing you do? For example, when I met Feynman at Los Alamos, I knew he was going to get a Nobel Prize. I didn't know what for. But I knew darn well he was going to do great work. No matter what directions came up in the future, this man would do great work. And sure enough, he did do great work. It isn't that you only do a little great work at this circumstance and that was luck, there are many opportunities sooner or later. There are a whole pail full of opportunities, of which, if you're in this situation, you seize one and you're great over there instead of over here. There is an element of luck, yes and no. Luck favors a prepared mind; luck favors a prepared person. It is not guaranteed; I don't guarantee success as being absolutely certain. I'd say luck changes the odds, but there is some definite control on the part of the individual.

Go forth, then, and do great work!



People have been saying that startup valuations are really high for about 3 years now.  I myself feel that they are high, but I have no idea when they are likely to change.

It’s mostly investors that talk about valuations being way too high.  But they’re the ones that keep willingly paying higher and higher prices.  In fact, they keep raising larger and larger funds.  So I think there has to be a discount rate on the claim.

The most important reason for this is simple capitalism—large pools of money look for the best risk-adjusted return.  Interest rates are effectively zero (and negative in Europe!) and will likely remain that way for awhile— the Fed has continually been too optimistic about when the economy will pick back up.   So fixed income is bad, and partially because of that, public equities, real estate, etc all feel really expensive.

The fundamental problem driving this lack of opportunity for capital, in my somewhat controversial opinion, is a lack of GDP growth.  Startups have growth, though, and so they attract investment interest.

There have been a lot of startup success stories in the last decade, and a lot more people want to invest in startups than ever before except maybe the 2000 bubble.  Crowdfunding (probably the most important new force in startup investing) is providing more competition for early-stage investments, and hedge funds and private equity firms are starting to do a lot more late-stage investing.  Angel investors are raising funds at an astonishing rate.   Some of these new investors invest partially for social status, not just a financial return, and so are willing to pay relatively higher prices.

A lot of these new investors are willing to accept lower returns than VC firms, given the alternative options for investing the capital.  But VC firms will continue to invest, of course, even if the prices are higher than they’d like. [1]

The number of good startups is increasing every year, but not as fast as the investment dollars are.  And so there is a supply and demand mismatch, and prices are going up.

VC has worked, at least partially, on special access and information asymmetry.  (VCs pitch their LPs about this and call it “competitive differentiation”.)  But access to startups has gotten much easier.  If you’re a VC firm still depending on this, you’re very likely failing. 

The good VCs are doing new things to remain on top.  Some firms are focusing on providing services like recruiting, business development, PR, and many others to their startups.   Some firms are trying to focus on having partners that are former founders.  Still others are trying to focus on contrarian investments.  All of this is great for founders.

A lot of the traditional “non-starter” terms from VCs are already going away.  We’re seeing more and more A rounds happen with less than 20% ownership going to the investors, and fewer and fewer requirements about investor control over the company.  Unfortunately, some good things are going away also.

It turns out to be really good for a company to have a board—it focuses the company if everyone knows they have to present the key metrics to outsiders once a month.  Some investors feel that if they own a smaller percentage of the company, they are willing to put in money but not time.  But I don’t think this strategy will work for long—if that’s the sales pitch, then founders will take the cheapest capital, and the crowd will probably pay more than VCs.  If I could ask VCs for only one thing in this new world, it’d be to keep showing up for board meetings. [2]

I believe good angel and venture investors really do add value, and most founders are rightly willing to take somewhat worse terms to work with people they believe will really help them.  But the capital markets are moving fast, and investors will have to keep up (this was part of our thinking about increasing the standard YC offer).

So what should founders do now that valuations are higher?

Definitely don’t start a company just because capital is available.  Remember that cheap capital doesn’t make starting a company much easier.  It only does stuff like drive up rent.  Success will still take a very long time.  And it’s definitely still bad to chase above-market valuations—you’ll price out people that will actually help.  Just take market terms and get back to work. 

Resist the urge to raise and spend too much money.  The track record of companies that raise $30MM or more in their first round is bad.  You may be one of the exceptions, but for a bunch of reasons, I think it’s better to have a small amount of money until everything is working, and only then really hit the gas pedal. 

Also, if capital feels cheap, it’s psychologically easier to spend.  It’s really important to stay frugal.  In addition to the often-discussed correlation of low CEO pay with success, I’ve noticed that frugal companies have a culture that ends up being much more focused on real results.  Frugal companies also tend to have a long-term focus.  And on a practical level, it’s always possible that the capital you’ve raised now will be the last you’ve ever raised.  You should treat it that way.

Some day the top-callers will be right.  It certainly feels to me like we may be in the early days of a bubble (though valuations for brand new companies, which felt most out of whack to me six months ago, seem to have come down somewhat).  And a macroeconomic collapse—which may happen—would certainly correct valuations in a hurry.  But unless some macro event happens, it feels like valuations can stay high.  Importantly, a lot of these startups are generating real revenue and earnings.



[1] My guess for what happens is that the great VCs continue to do well.   Many investors think new startups will be worth more than most of the startups from ten years ago—markets keep getting bigger, more good people are starting startups, startups are becoming easier to start, distribution keeps getting easier, and interest rates will probably stay low—or it’s possible that VCs will generate still good but lower-than-historical returns.

[2] The increase in valuations has led to some funny new behaviors.  One of the funniest examples is a simultaneous obsession with the price other investors are paying—“Even though I thought this price was good yesterday, I found out someone else is getting to invest at a lower price and I’m furious”—coupled with a refrain of “I’ll work really hard for the company and add much more value than your other investors, so I’d like advisory shares or a discount to participate in your round”.  I hope investors will stop doing these sorts of things. 

Founder Depression

If you ask a founder how her startup is going, the answer is almost always some version of “Great!”

There is a huge amount of pressure as a founder to never show weakness and to be the cheerleader in all internal and external situations.  The world can be falling down around you—and most of the time when you’re running a company, it is—and you have to be the strong, confident, and optimistic.  Failing is terrifying, and so is looking stupid.

Founders end up with a lot of weight on their shoulders—their employees and their families, their customers, their investors, etc.  Founders usually feel a responsibility to make everyone happy, even though interests are often opposed.  And it’s lonely in a way that’s difficult to explain, even with a cofounder (one of the things that works about organizations like Y Combinator is that you have a peer group you can lean on for support).

So a lot of founders end up pretty depressed at one point or another, and they generally don’t talk to anyone about it.  Often companies don’t survive these dark times. 

Failing sucks—there is no way to sugarcoat that.  But startups are not life-and-death matters—it’s just work.

Most of the founders I know have had seriously dark times, and usually felt like there was no one they could turn to.  For whatever it’s worth, you’re not alone, and you shouldn’t be ashamed.

You’ll be surprised how much better you feel just by talking to people about the struggles you’re facing instead of saying “we’re crushing it”.  You’ll also be surprised how much you find other founders are willing to listen.

Bitcoin Price Pressure

The price of bitcoin keeps trending down.  [1] This causes a lot of people to declare the end of bitcoin.

It’s important to understand that the default price pressure of the bitcoin ecosystem is down.  There are a lot of reasons for this, so I’ll just give a few examples. 

When most merchants take bitcoin for a purchase, they immediately sell for dollars (they can’t usually pay their vendors in bitcoin, they can’t pay tax in bitcoin, they don’t want to be exposed to the volatility, etc.)

When miners mine bitcoin, they have to sell some of them to pay for the electricity in dollars (or, more likely, RMB).  As the difficulty goes up and the price of bitcoin goes down, they have to sell a larger and larger percentage of what they mine.  In fact, as far as I can tell, mining is currently unprofitable with any reasonable cost of electricity.  It still makes sense to mine if you’re living in a dorm and don’t pay for electricity, or if you can’t pass a KYC check and are willing to pay a big premium to get bitcoin.

The recent US and international tax changes and tax filings also caused sell pressure.  This will continue to be the case until the US government takes bitcoin for taxes.  If I ran the government, I would never do this—the US needs the dollar to remain the world reserve currency.

There are plenty of other reasons, but the point is that bitcoin is different from many other financial markets, where the default pressure is up. [2]

This doesn’t mean bitcoin is doomed.  It just means that for it to succeed, we’ll need significant external buy pressure.  As I wrote awhile ago, I think the key thing we need for this is people actually using bitcoin for transactions instead of speculation (and merchants willing to hold bitcoin balances). [3] Unfortunately, transaction volume still appears to be trending down. [4] Anecdotally, I hear from merchants who start taking bitcoin that after an initial spike they see almost no volume.

The other way to get enough buy pressure would be if many people started deciding they want to hold bitcoin as a hedge or a speculation.  This spurs occasional bubbles, but we haven’t yet seen it work long term.

A declining bitcoin price does not mean bitcoin is failing.  And even if bitcoin itself fails, I think the blockchain will be one of key technical innovations of this time period.  In fact, in the most recent set of YC interviews, we saw more great blockchain companies than bitcoin companies.  Maybe Ripple or Dogecoin ends up winning. [5] Or maybe something that hasn’t been invented yet.

But it’s hard to imagine a future where the blockchain concept isn’t really important.



[2] Paul Buchheit first made this point:



[5] Speaking of dogecoin, as of this writing, it is the number 3 crytocurrency measured by daily volume, and if the market cap went up $10MM (about 25%), it would be the number 3 by market cap also.

Employee Equity

Startup employees often do not get treated very well when it comes to stock compensation.   New ideas float around occasionally, but lawyers are usually averse to trying new things, and investors don’t feel that they have enough incentive to try something new for employees.

There are four major problems: 

1) Employees usually don’t get enough stock. 

2) If an employee leaves the company, he or she often can’t afford to exercise and pay taxes on their options. 

3) Employee options sometimes get unfavorable tax treatment.

4) Employees usually don’t have enough information about the stock or options. 

Here are some proposed solutions:

1) Startups should give employees more stock.  Value is created over many, many years.  Founders certainly deserve a huge premium for starting the earliest, but probably not 100 or 200x what employee number 5 gets.  Additionally, companies can now get more done with less people.

It’s very difficult to put precise numbers on this because the specifics of every situation matter so much.  Perhaps the best way to think about it is to try to come up with a total compensation package with the same expected value (using the company valuation of the last round, or a best-efforts guess if it’s been a long time since the round) as the employee would get at a big company like Google.  As an extremely rough stab at actual numbers, I think a company ought to be giving at least 10% in total to the first 10 employees, 5% to the next 20, and 5% to the next 50.  In practice, the optimal numbers may be much higher.

One problem is that startups try to have very small option pools after their A rounds, because the dilution only comes from the founders and not the investors in most A-round term sheets.  The right thing to do would be to increase the size of the option pool post-A round, but unfortunately this rarely happens—no one wants to dilute themselves more, and this leads to short-sighted stinginess much of the time.

Option pools are complete fiction; boards can increase them whenever they want.  It should never be used as a reason for not making a grant.

2) Most employees only have 90 days after they leave a job to exercise their options.  Unfortunately, this requires money to cover the strike price and the tax bill due for the year of exercise (which is calculated on the difference between the strike and the current FMV).  This is often more cash than an employee has, and so the employee often has to choose between walking away from vested options he or she can’t afford to exercise, or being locked into staying at the company.  It’s a particularly bad situation when an employee gets terminated.

This doesn’t seem fair.  The best solution I have heard is from Adam D’Angelo at Quora.  The idea is to grant options that are exercisable for 10 years from the grant date, which should cover nearly all cases (i.e. the company will probably either go public, get acquired, or die in that time frame, and so either the employee will have the liquidity to exercise or it won’t matter.)  There are some tricky issues around this—for example, the options will automatically convert from ISOs to NSOs 3 months after employment terminates (if applicable) but it’s still far better than just losing the assets.  I think this is a policy all startups should adopt.

As an aside, some companies now write in a repurchase right on vested shares at the current common price when an employee leaves.  It’s fine if the company wants to offer to repurchase the shares, but it’s horrible for the company to be able to demand this.

3) Tax treatment on ISOs sounds good, but there’s an issue with AMT (Alternative Minimum Tax) and employees often end up paying more tax than they were expecting.   NSO gains are taxed as ordinary income.  RSU gains are also taxed as ordinary income.

Tax optimization is a second-order issue, and for an immediate solution, I think extending exercise windows to 10 years is the most important thing to do.  But longer-term, we should figure out a way for employees to be taxed on their stock compensation the same way as founders (whether or not capital gains should be taxed less than ordinary income is a separate discussion, but in any case I think the tax treatment should be the same). 

I think this may be doable.  Ideally, employees would just get restricted stock (not RSUs), and then when they sold it’d be taxed as long-term capital gains.  The problem is that as the company grows, the stock has a non-trivial present value, and if an employee were granted stock then they would then owe immediate tax on the value of the grant.

I think there are a lot of ways to fix this.  The easiest would be if the IRS would agree to not tax illiquid private stock until it gets sold, and then tax the gain from the basis as long-term capital gains and the original value as ordinary income.

Another might be to create a new class of employee stock.  Today, in an early-stage company, common shares are usually worth much less than preferred shares.  It might be possible to create a class of shares with less rights than common and thus worth even less.  The idea would be to convert these shares into common on an acquisition or IPO, but before that, they would be non-transferable and have no value.  If it were possible to create a class of stock that the IRS agreed had next to zero value, it might be possible to grant employees this sort of stock, have them owe a tiny bit of tax on it now, and then have normal long-term capital gains treatment years later when the startup goes public. 

4) Most startups do a bad job of helping employees think about the value of their options.  At a minimum, any startup should tell a prospective employee what percentage of the company the equity grant represents (number of shares is meaningless).  Some startups are very hesitant to do this—they don’t want to disclose the number of shares outstanding.  Employees should demand to know what percentage of the fully-diluted shares their stock options represent, and be very suspect of any startup that won’t tell them.

A specific question worth asking is some version of “so if I have 0.5% of company and it gets acquired tomorrow for $100 million dollars, will I get $500,000?”  There are many ways for this not to be the  case—there can be a huge liquidation preference, for example—that most employees don’t know to think about.  So it’s worth asking about a specific scenario.

While you’re asking questions, another good one to ask is “how much money did the company lose last month, and how much is in the bank?”  This is better than asking how much runway the company has, because most founders calculate that off of a plan that assumes revenue growth which does not always materialize.


I have two other thoughts about stock-based compensation at startups.

First, I think employee stock and options should usually not be transferrable.  It causes considerable problems for companies when employees sell their stock or options, or pledge them against a loan, or design any other transaction where they agree to potentially let someone else have their shares or proceeds from their shares in the future in exchange for money today.

I think it’s fair that if founders sell stock, they should offer an opportunity to employees that have been at the company for more than a certain number of years to sell some portion of their shares.  And some companies offer an employee liquidity program even when the founders don’t sell any shares themselves.  But otherwise, I think it’s reasonable for employees to wait for an acquisition or IPO.

Second, I think it’s time to consider other vesting ideas.  The standard at startups is 4 years with a 1-year cliff.  So you get 25% of your options after you’ve been there for a year, and 62.5% if you leave after 2.5 years.

It’s possible that 4 years is now too short—companies are often worth more than they were 10 years ago, but they take longer to reach liquidity.  I’ve seen some startups offer 5 or 6 year vesting schedules.  To compensate for this, they offer above-market grants.

Another structure I’ve seen is back-weighted vesting.  For example, 10% of the grant vests after the first year, and then 20%, 30%, 40% in the following years.  Again, the startups I know that do this tie it to above-market grants, and I think it helps them select for employees that really believe in the company and want to be there for a long time. (Also, companies that have vesting schedules like this usually do it for founders too.)

Finally, a third structure I’ve seen is a new way of thinking about refresher grants.  For a company using options, it’s nice to grant employees options early while the strike is low.  It’s possible to give “forward-dated grants”—i.e., you can give a high-performing employee a refresher grant today where 1/3 of it starts vesting immediately and the other 2/3 starts vesting when their initial grant is fully vested.  This guarantees them a low-strike price and presumably a relatively large grant in a few years.  Dustin Moskovitz at Asana does something like this, and I think it makes a lot of sense.

These are just a few of the ideas I’ve seen about new ideas for employee vesting.  But I think they’re worth considering—the default 4-year grant does not seem to be the best option.

The Worst Part of YC

We are going to send out YC summer 2014 interview decisions (both yes and no) before 10 pm PDT tonight.

The worst part of our job at YC is rejecting companies.  It leaves me feeling down for many days after our application process.  I experienced plenty of rejection from investors while running my own startup, and I remember well how bad it is.  Starting a startup is such a hard thing that we wish we could help everyone doing so.

Some day, we hope to be able to fund almost all the good startups.  In the meantime, we still have capacity constraints as we figure out how to scale, and that means we’re stuck saying no to potentially good companies.

The best startups often look bad at this stage, and we make mistakes.  We could easily miss something great.  If you’re working on something that users love, you like working on it, and you have a plan for how to build a business around it, then please don’t let us deter you.  (It's sometimes useful to ask friends for an outside perspective on how you're doing.)

Although we had nearly 20% more applications than a year ago, it was really striking how much higher the average quality of applications was for this batch compared to any previous batch.  Most of the partners independently mentioned this to me.

Anyway, to everyone we’re unable to fund: Best of luck, and don’t give up.  We love to see founders and companies reapply—companies that look bad now can look great with 6 months of progress.

Startups, Role Models, Risk, and Y Combinator

The YC application deadline is this Friday, and you can apply here.

People often tell us they think they want to start a company but just aren’t sure, so I thought I’d share some thoughts.  Although it’s true that most people aren’t well suited to start startups, a lot of people that could be great at it are afraid to make the leap.  They look at super successful founders who now seem impossibly impressive.

The first time I met the Airbnb founders they were clearly smart and fairly impressive, but nothing like what they are today.  We met at a coffeeshop in Mountain View, and they were stumbling over their words and talking about how things weren’t going that well.  Now they are taking over the world.  This improvement is not a special case—the same thing happened for the Collison brothers at Stripe, and the founders of Homejoy, Weebly, Coinbase, Teespring, Pebble, and on and on and on.

Here’s the secret: everyone starting a startup for the first time is scared, and everyone feels like a bit of an imposter.  Even the most successful founders doubt themselves and their startups many times in the early days.  But founders improve very quickly.

So when you’re thinking about whether or not you can start a startup, remember that you shouldn’t compare yourself to these people now.  They became much more impressive in the course of running of their startup, and so can you.

Starting a startup is very hard and very painful.  Success usually requires a level of determination and commitment for which most people don’t have a mental model.

For example, when Adora Cheung was starting Homejoy, she would work all day as a cleaner to learn the business, drive an hour back to Mountain View, stay up as late as she could coding, then drive back to San Francisco at ~3am to beat traffic, sleep in her car, and do it again.  She also gave both her apartment and her car to early cleaners so that they could partner up with Homejoy.  We don’t want to delude anyone about what running a startup is like—it’s a rational decision to decide you don’t want to start a startup.  

But there are lots of great reasons to start a company, and a lot of people are willing to accept the pain. The unfortunate situation is when people who want to start startups don’t actually get started—they feel like the great startup founders are too impressive, or they don’t know what to do, or it’s too risky.

It’s really not that risky—in general, few things are as risky as they seem.  And Y Combinator makes it even less risky—we don’t invest much money, but it’s enough to live on (even with a family in most cases).  If the startup doesn’t work out, one of the advantages of the alumni network is that most YC founders find something interesting to do next.

The only thing you have to know how to do is build something people want.  If you can do this, and you are sufficiently relentless, you can probably create more value and have more impact than you could in a regular job.  YC can teach you nearly everything else—in fact, most of what we do is give startups one-on-one advice.

Founders are usually amazed by how much they get done over the three months of YC, and how much they change.  The structure of YC helps startups focus on the few things that matter, and a group of people that mostly start out feeling like they don’t belong transform to some of the best founders out there.

If you’re still on the fence about applying for the Summer 2014 YC batch, we hope you’ll make the leap!  And don’t worry if you’re not as far along as you’d like of if your application isn’t polished enough.  We’ve gotten very good at looking past this, and also it doesn’t hurt you if you don’t get in the first time you apply (we rejected Drew Houston from Dropbox the first time he applied).  We fund companies at all stages, from just the faintest idea to post-Series B. 

Here is some advice other people have written about how to apply:

How to Apply to Y Combinator by Paul Graham

Last Minute Advice for YC Applicants by Garry Tan

Harj Taggar on Quora answering "What is the best advice for a startup applying to Y Combinator?"

Michelle Crosby on her YC experience

Drew Houston's Dropbox Application

Harry Zhang's (Lob YC S13) Advice for YC Applicants 

 Y Combinator Applicant Advice by Zain Shah

What I've Learned From Female Founders So Far

On the whole, I got a great response to my request for feedback about how YC could encourage female founders.  It's clear there are two separate problems: 

1) Some women already starting startups aren't interested in doing Y Combinator.

2) Some women who could be great founders don't start startups. 

I realize it's always a bit ridiculous for a guy to talk about what it's like for female founders, but I'm interested in doing whatever I can to help, because the venture business has definitely been unfair to women.  The women on our team also care deeply about this issue, and  can do more than I can to address it.

For point #1, one of the most consistent messages was that we need to make it clear that we care about the issue and want to fund more female founders.  So I'll say that now: we want to fund more women.  And we'll keep saying this in the outreach we do.

We want to fund more women because it's the right thing to do, but we're not doing this for diversity's sake alone.  We want to fund more women because we are greedy in the good way--we want to fund the most successful startups, and many of those are going to be founded by women.

Many are also going to be founded by people of different races, different religions, from different countries, straight, gay, in their 20s, or in their 50s.  All of those apply to people in the current YC batch.  In fact, they all apply to the YC partnership as well.  Again, we don't do this for the sake of diversity. We do it because we want to get the best people, whatever they're like.

In the current YC batch, 24% of the companies we funded have one or more female founders, and there will be a lot of companies out of those with the potential to serve as role models.  We hope that as the number of female YC alumni continues to rise, more women will feel YC is a place that supports and respects them.

Another message was that we should do more to make women feel welcome.  Many emails pointed out that our website shows nearly all men; we'll fix that.  We'll also continue to work with our most successful female founders to talk about their experiences and mentor women that could be future founders.  We'll continue to ask women to come speak at dinners. In this batch, two of my four favorite speakers were women (Adora Cheung and Julia Hartz).  And we're working on something to improve the quality of Hacker News comments.

A very common request was for us to have women in the interviews we do before funding companies.  In the last batch, we had a woman in 2 of the 3 interview tracks.  We now have more female YC partners, so for this upcoming batch, we'll have a woman in every track.

Nearly all women who emailed me suggested that we keep the exact same bar for women as for men (anything else wouldn't be fair to the incredible women we fund every batch), but many pointed out that women are often good in different ways and at different things than men--for example, that men and women express confidence differently--and that we should make sure our criteria catch that.

A specific issue that came up is a belief that we look for founders that look like Mark Zuckerberg.  Actually that meme began as a self-deprecating joke. We funded a guy once who looked like Mark but ended up doing badly, and when PG was asked by a reporter how to fool him, he said that apparently this was one way. His real point was that looking like Zuckerberg means nothing--that you can look remarkably like him and still fail miserably.  I think it's more accurate to say we look for founders that have some of the qualities that have made Zuckerberg so successful.

Finally, I heard a lot of support for events like the Female Founders Conference and a belief that they could help change the industry.  And if YC continues to fund more women, many people believe VCs will follow.

For point #2, I think we can do a lot to reach young women earlier and help teach them about startups and coding.  Many women pointed out that you don't have to be a coder to be a founder.  That's definitely true, and it was a good reminder for me personally.  But I think it's good to at least present learning to code as an option worth considering.

As we do more events, we'll continue to reach out to women.  Kat, our director of outreach, Jessica, our founding partner, and I will all specifically work on this.  For example, we're thinking about holding a hackathon later this year.  It'd be great to have a lot of women attend.

We're also going to ask some of our successful female founders to do more outreach.  I believe we have already funded at least one female founder/CEO who will produce a multibillion dollar company. She and others are outstanding role models.

There's lots of work still to do, but we're on it.  I hope other investors will join us.

New RFS -- Breakthrough Technologies

We’d like for Y Combinator to fund more breakthrough technology companies—companies that solve an important problem, have a very long time horizon, and are based on an underlying technological or scientific breakthrough.  Not many people try to start these companies, so starting a company that will require a huge amount of time and money is an automatic competitive advantage.  SpaceX and Tesla are great examples of what is possible.

It used to be the case that governments funded a lot of development of breakthrough technologies.  The bad news is that they have mostly stopped; the good news is that the leverage of technology is such that now small startups can do what used to take the resources of nations. [1]

We think the YC model works well for these companies.  We invest with infinite time horizon and are not afraid of risky-looking companies. [2] We understand software, which will be central to many of these companies.  We are good at getting companies to focus on solving real problems for real customers, and not just developing technology for its own sake.  And our model helps companies figure out a right-sized initial project achievable with a small amount of time and money—great companies get built with a series of small wins that compound over time, and early momentum is critical.  A common failure mode of many ambitious companies is to bite off an initial project that is far too big and expensive.  Finally, we know a lot about raising money, which will be a big part of the challenge for many of these companies as they mature.

Here is a list (we’ll add to it over time) of some areas we’re particularly interested in, but more generally, we’ll pay attention to any area where technology can make the world much better.

Energy.  There is a remarkable correlation between the cost of energy and quality of life.  Throughout history, when the cost of energy has come down a lot (for example, with the steam engine) the quality of life goes up a lot.

Cheap energy would do a huge amount to reduce poverty.  New energy sources could also help the environment, the economy, reduce war, ensure a stable future, make food and water more abundant, and much more.

We believe economics will dominate—new sources must be cheaper than old ones, without subsidies, and be able to scale to global demand.

Nuclear energy can hit the bid, and possibly so can renewables.  But pricing is the first order question.

In addition to generation, we’re also interested in energy storage and transmission.  10x better batteries would enable great new things, as would the ability to easily move energy around. 

AI. Relative to the potential impact, it doesn’t seem like enough smart people are working on this.

A lot of smart people talk about AI with a combination of awe and fear, both for good reasons.  But it feels like it could be one of the dividing lines in the history of technology, where before and after look totally different.

Robotics. Robots will be a major way we get things done in the physical world.  Our definition is pretty broad—for example, we count a self-driving car as a robot.  Robots are how we’ll likely explore space and maybe even the human body.

Biotech. It’s still early, but it seems like we’re finally making real progress hacking biology.  There are so many directions this can go—fighting disease, slowing aging, merging humans and computers, downloading memories, genetic programming, etc.   We are certain that this is going to be a surprising, powerful and controversial field over the next several decades—it feels a little bit like microcomputers in the 1970s. 

Healthcare. Healthcare in the United States is badly broken.  We are getting close to spending 20% of our GDP on healthcare; this is unsustainable.

We’re interested in ways to make healthcare better for less money, not in companies that are able to exploit the system by overcharging.  We’re especially interested in preventative healthcare, as this is probably the highest-leverage way to improve health.  Sensors and data are interesting in lots of different areas, but especially for healthcare.

Food and water. At some point, we are going to have problems with food and water availability.  Technology can almost certainly improve this.  Great innovations are possible—we will need another advancement on the scale of what Norman Borlaug did. 

Education. If we can fix education, we can eventually do everything else on this list.  The first attempts to use technology to fix education have focused on using the Internet to distribute traditional content to a wider audience.  This is good, but the Internet is a fundamentally different medium and capable of much more.

Solutions that combine the mass scale of technology with one-on-one in-person interaction are particularly interesting to us.

This may not require a “breakthrough technology” in the classical sense, but at a minimum it will require very new ways of doing things. 

Internet Infrastructure.  We can’t imagine life without the Internet.  We need to be sure it keeps working—this includes everything from security to free and open communication to infrastructure.  The Internet is a transformative power, and we’re particularly interested in applications that transform the big underpinnings of society (bitcoin is a great example!).  The Internet lets people around the world coordinate action—there are almost certainly important businesses to be built around this concept.

Of particular interest to us are ways to use the Internet to fix government—for example, crowdfunding social services.

An important trend is the API-ification of everything.  As more and more businesses are accessible with a web API, the Internet becomes more and more powerful. 

Levers.  We’re interested in technology that multiplies the efforts and productivity of individuals.  Robots are a great example, but this also includes areas like new programming languages, powered exoskeletons, augmented reality, etc.

Science.  Science seems broken.  The current funding models are broken and favor political skill over scientific genius.  We need new business models for basic research.  There are a lot of areas where scientific developments can have huge commercial applications—materials, neuroscience, climate engineering, and cheaper/better ways to get to space, just to name a few—and we’d love to figure out a way for it to happen.  Bell Labs worked a long time ago but would probably not work in today’s world.

Transportation and housing.  About half of all energy is used on transportation, and people spend a huge amount of time unhappily commuting.  Face-to-face interaction is still really important; people still need to move around.  And housing continues to get more expensive, partially due to difficulties in transportation.  We’re interested in better ways for people to live somewhere nice, work together, and have easier commutes.

As a side note, you shouldn’t start a company just because it’s on this list.  Our hope is that someone already working on a company in one of these areas that might not have otherwise applied to YC will now consider it.  The great majority of the startups we fund will continue to be the sort of Internet and mobile companies we’ve funded in the past, so if that’s what you wanted to do before this post, keep doing it.  Traditional-looking startups like Google and Facebook are obviously as important as any company one could imagine, and clearly are breakthrough technologies. 

[1] To be clear, we are not interested in funding patent trolls.  We only want to fund businesses that actually solve problems and create value. 

[2] Related to long time horizons, if a company needs to raise a billion dollars of funding over the course of its life, that doesn’t scare us—in fact, that’s a plus.