§Humbly aim high?

A poem “The Church-Porch,” by George Herbert (1593–1633) (link).

Pitch thy behaviour low, thy projects high;
So shalt thou humble and magnanimous be:
Sink not in spirit; who aimeth at the sky,
Shoots higher much, than he that means a tree.
A grain of glory mix’d with humbleness
Cures both a Fever, and Lethargickness.

§Work in AI?

Stuart Russell and Peter Norvig write a call to action in the introduction to Artificial Intelligence: A Modern Approach. The advertisement has changed over the years to reflect cultural changes and the increased impact of AI systems on the world. However, it appears that the positions have not yet been filled.

First edition, 1995:

AI is one of the newest disciplines. It was formally initiated in 1956, when the name was coined, although at that point work had been under way for about five years. Along with modern genetics, it is regularly cited as the “field I would most like to be in” by scientists in other disciplines. A student in physics might reasonably feel that all the good ideas have already been taken by Galileo, Newton, Einstein, and the rest, and that it takes many years of study before one can contribute new ideas. AI, on the other hand, still has openings for a full time Einstein.

Second edition, 2003:

AI is one of the newest sciences. Work started in earnest soon after World War II, and the name itself was coined in 1956. Along with molecular biology, AI is regularly cited as the “field I would most like to be in” by scientists in other disciplines. A student in physics might reasonably feel that all the good ideas have already been taken by Galileo, Newton, Einstein, and the rest. AI, on the other hand, still has openings for several full-time Einsteins.

Third edition, 2010:

AI is one of the newest fields in science and engineering. Work started in earnest soon after World War II, and the name itself was coined in 1956. Along with molecular biology, AI is regularly cited as the “field I would most like to be in” by scientists in other disciplines. A student in physics might reasonably feel that all the good ideas have already been taken by Galileo, Newton, Einstein, and the rest. AI, on the other hand, still has openings for several full-time Einsteins and Edisons.

Fourth edition, 2022:

Surveys regularly rank AI as one of the most interesting and fastest-growing fields, and it is already generating over a trillion dollars a year in revenue. AI expert Kai-Fu Lee predicts that its impact will be “more than anything in the history of mankind.” Moreover, the intellectual frontiers of AI are wide open. Whereas a student of an older science such as physics might feel that the best ideas have already been discovered by Galileo, Newton, Curie, Einstein, and the rest, AI still has many openings for full-time masterminds.

§Seek important problems?

Richard Hamming in a talk You and Your Research, Bell Communications Research Colloquium Seminar (link):

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!

(There is more advice about other aspects of how to do good work in the rest of the talk.)

§Avoid the crowd?

Marvin Minsky in 6.868J The Society of Mind, 2011, lecture 1 (link):

… almost all young people who start working on artificial intelligence look around and say “what’s popular? statistical learning… so I’ll do that!” that’s exactly the way to kill yourself scientifically. You don’t want to get the most popular thing. You want to see, “what am I really good at, that’s different, and what are the chances that that would provide another thing?”

Donald Knuth in an interview, “A Life’s Work Interrupted,” Communications of the ACM, 51(8):31–35 (link). Page 35:

When I was working on typography, it wasn’t fashionable for a computer science professor to do typography, but I thought it was important and a beautiful subject. Other people later told me that they’re so glad I put a few years into it, because it made it academically respectable, and now they could work on it themselves. They were afraid to do it themselves. When my books came out, they weren’t copies of any other books. They always were something that hadn’t been fashionable to do, but they corresponded to my own perception of what ought to be done. Don’t just do trendy stuff. If something is really popular, I tend to think: back off. I tell myself and my students to go with your own aesthetics, what you think is important. Don’t do what you think other people think you want to do, but what you really want to do yourself. That’s been a guiding heuristic for me all the way through.

§Raise the sea?

Alexander Grothendiek in Récoltes et Semailles, 1985–87, page 553, translated by Colin McLarty (link):

I can illustrate the second approach with the same image of a nut to be opened. The first analogy that came to my mind is of immersing the nut in some softening liquid, and why not simply water? From time to time you rub so the liquid penetrates better, and otherwise you let time pass. The shell becomes more flexible through weeks and months—when the time is ripe, hand pressure is enough, the shell opens like a perfectly ripened avocado!

A different image came to me a few weeks ago. The unknown thing to be known appeared to me as some stretch of earth or hard marl, resisting penetration… the sea advances insensibly in silence, nothing seems to happen, nothing moves, the water is so far off you hardly hear it… yet it finally surrounds the resistant substance.

§Have an irresistible impulse to create?

Norbert Wiener in The Human Use of Human Beings, 1954, pages 133–134:

Properly speaking the artist, the writer, and the scientist should be moved by such an irresistible impulse to create that, even if they were not being paid for their work, they would be willing to pay to get the chance to do it. However, we are in a period in which forms have largely superseded education content and one which is moving towards an ever-increasing thinness of educational content. It is now considered perhaps more a matter of social prestige to obtain a higher degree and follow what may be regarded as a cultural career, than a matter of any deep impulse.

In view of this great bulk of semi-mature apprentices who are being put on the market, the problem of giving them some colorable material to work on has assumed an overwhelming importance. Theoretically they should find their own material, but the big business of modern advanced education cannot be operated under this relatively low pressure. Thus the earlier stages of creative work, whether in the arts or in the sciences, which should properly be governed by a great desire on the part of the students to create something and to communicate it to the world at large, are now subject instead to the formal requirements of finding Ph.D. theses or similar apprentice media.

Some of my friends have even asserted that a Ph.D. thesis should be the greatest scientific work a man has ever done and perhaps ever will do, and should wait until he is thoroughly able to state his life work. I do not go along with this. I mean merely that if the thesis is not in fact such an overwhelming task, it should at least be in intention the gateway to vigorous creative work. Lord only knows that there are enough problems yet to be solved, books to be written, and music to be composed! Yet for all but a very few, the path to these lies through the performance of perfunctory tasks which in nine cases out of ten have no compelling reason to be performed. Heaven save us from the first novels which are written because a young man desires the prestige of being a novelist rather than because he has something to say! Heaven save us likewise from the mathematical papers which are correct and elegant but without body or spirit. Heaven save us above all from the snobbery which not only admits the possibility of this thin and perfunctory work, but which cries out in a spirit of shrinking arrogance against the competition of vigor and ideas, wherever these may be found!