DACHVARD

Talk delivered at Bell Laboratories, circa 1952.

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A very small percentage of the population produces the greatest proportion of the important ideas. This is akin to an idea presented by the mathematician Turing — that the human brain is something like a piece of uranium. If the uranium is below the critical mass and you shoot one neutron into it, nothing much happens. But increase the size, push it past the threshold, and you get an explosive chain reaction. Turing said ideas in the human brain work similarly.

There are some people who, if you shoot one idea into the brain, you will get half an idea out. There are other people who are beyond the critical point — they produce two ideas for each idea sent in. Those are the people beyond the knee of the curve.

When you think that Newton, at the age of 25, had produced enough science, physics, and mathematics to make ten or twenty men famous — the binomial theorem, differential and integral calculus, the laws of gravitation, the laws of motion, the decomposition of white light — you begin to wonder: what pushes a person to that part of the curve?

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Three Prerequisites

I think we can set down three things that are fairly necessary for scientific research, or for any sort of inventing — mathematics, physics, anything along that line. I don't think a person can get along without any one of them.

Training and Experience

The first is obvious. You don't expect a lawyer, however bright he may be, to give you a new theory of physics these days. You have to know the field.

Intelligence

The second is a certain amount of intelligence or talent. You have to have an IQ that is fairly high to do good research work. I don't think there is any good engineer or scientist who can get along on an IQ of 100, which is the average for human beings. This, we might say, is a matter of heredity; training is a matter of environment.

Motivation

Those two are not sufficient. The third component is the one that makes an Einstein or a Newton. For want of a better word: motivation.

You have to have some kind of drive, some desire to find out the answer — a desire to find out what makes things tick. If you don't have that, you may have all the training and intelligence in the world and you won't find answers, because you won't ask questions.

This motivation has several faces. First, curiosity — he wants to know the answers, he's just curious how things tick, and if he sees something strange, he wants to raise questions.

Then there's constructive dissatisfaction — not the pessimistic kind, not "I don't like the way things are," but something closer to: "This is OK, but I think things could be done better. I think there is a neater way to do this." There is continually a slight irritation when things don't look quite right, and I think that dissatisfaction is a key driving force in good scientists.

And then there is the pleasure in results — the sheer satisfaction of the thing. I get a big kick out of proving a theorem I've been working on for a week. I get a kick out of seeing a clever circuit design that uses very little equipment and gets apparently a great deal of result. It is maybe a little like what Fats Waller said about swing music: "Either you got it or you ain't."

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Six Techniques

Supposing a person has these three properties — are there any tricks, any gimmicks, that actually aid in creative work? I think there are, and I think they can be catalogued. If one consciously applied these to various problems, in many cases you'd find solutions faster than you would normally — or find solutions in cases where you might not find them at all.

Good research workers apply these things unconsciously and automatically. If they were brought forth into conscious thinking — here is a situation where I would try this method of approach — that would probably get there faster.

I. Simplification

When given a problem, probably the most powerful approach is to try to eliminate everything except the essentials — cut it down to size. Almost every problem is befuddled with extraneous data of one sort or another. If you can bring it down to its main issues, you see more clearly what you're trying to do.

In doing so, you may have stripped away the problem you were after. You may have simplified it to the point that it doesn't resemble the original. But very often, if you can solve the simple problem, you can add refinements to the solution until you get back to the one you started with.

II. Analogous Problems

You have a problem P and a solution S which you don't know yet.

But if you have experience in the field, you may know of a somewhat similar problem P' which has already been solved and has a known solution S'. All you need to do is find the analogy from P' to P — and the same analogy will carry you from S' to S.

This is the reason why experience in a field is so important. Your mental matrix fills up with P's and S's. You can find one tolerably close to the P you're trying to solve, step across to the corresponding S', and work back to the S you're after. It seems to be much easier to make two small jumps than one big jump.

III. Restate the Problem

For a given problem, try to restate it in as many different forms as you can. Change the words. Change the viewpoint. Look at it from every possible angle. After you've done that, try to look at it from several angles simultaneously — perhaps you'll get an insight into the real basic issues.

If you don't do this, it is very easy to get into ruts of mental thinking. You start with a problem, go around in a circle, and if you could only get over to a slightly different vantage point, you would see your way clear — but you can't break loose from mental blocks. This is why someone quite new to a problem will sometimes look at it and find the solution immediately, while you have been laboring for months. They see it from a fresh viewpoint.

IV. Generalization

This is very powerful in mathematical research. Someone proves a special result in two dimensions, and immediately someone else generalizes it to N dimensions. Someone proves something for real numbers, and someone extends it to a general algebraic field.

This is actually quite easy to do if you only remember to do it. The minute you've found an answer to something, ask yourself: can I generalize this? Can I make a broader statement that includes more? In engineering: can I apply the same clever principle to a larger class of problems? Is there anywhere else I can use this idea?

V. Structural Analysis

Sometimes the jump from problem to solution is too large to take in one step. Break it down. Set up a path through the domain — a sequence of subsidiary results, 1, 2, 3, 4 — and prove each one in turn until you arrive at the final solution.

Many proofs in mathematics have been found by extremely roundabout processes. A man starts to prove a theorem, wanders all over the map, proves results that don't seem to lead anywhere — and then eventually ends up by the back door on the solution. Very often, once you've found it, you can simplify: you see shortcuts you couldn't see before, steps that were superfluous, a more direct path that only becomes visible after you've found any path at all.

VI. Inversion

You are trying to obtain solution S on the basis of premises P, and you can't do it. Turn the problem over. Suppose that S were the given proposition — the axioms, the known quantities — and what you are trying to obtain is P. Just imagine that were the case. Often you will find it is relatively easy to solve the problem in that direction.

If so, it is often possible to invert it in small stages — relay by relay, step by step — until you have found the path in the reverse direction, and from that, the path in the original.

I once had the experience of designing a machine that played the game of nim. It seemed quite difficult in the forward direction, requiring many relays. But then I got the idea that if I inverted the problem — if the given and required results had been interchanged — it would be very easy. That idea led to a far simpler design. The machine worked backward: it started with the required result and ran it back until it matched the given input. The solution came by inverting the direction of thought entirely.

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Now this is perhaps all very philosophical and abstract. I'd like to show you the machine I brought along, and go into one or two of the problems connected with its design — because I think they illustrate some of these things better than words do. If you'll all come up around the table, we can have a look at it.