“I think the theory is simply a way to sweep the difficulties under the rug,” Richard Feynman said. “I am, of course, not sure of that.” It sounds like the kind of criticism, ritually tempered, that comes from the audience after a controversial paper is presented at a scientific conference. But Feynman was at the podium, delivering a Nobel Prize winner’s address. The theory he was questioning, quantum electrodynamics, has recently been called “the most precise ever devised”; its predictions are routinely verified to within one part in a million. When Feynman, Julian Schwinger, and Sin-Itiro Tomonaga independently developed it in the 1940s, their colleagues hailed it as “the great cleanup”: a resolution of long-standing problems, and a rigorous fusion of the century’s two great ideas in physics, relativity and quantum mechanics.
Feynman has combined theoretical brilliance and irreverent skepticism throughout his career. In 1942, after taking his doctorate at Princeton with John Wheeler, he was tapped for the Manhattan Project. At Los Alamos, he was a twenty-five-year-old whiz kid, awed neither by the titans of physics around him (Niels Bohr, Enrico Fermi, Hans Bethe) nor by the top-secret urgency of the project. The security staff was unnerved by his facility at opening safes–sometimes by listening to the tiny movements of the lock mechanism, sometimes by guessing which physical constant the safe’s user had chosen as the combination. (Feynman hasn’t changed since then; many of his students at Caltech have acquired safe-cracking skills along with their physics.)
After the war, Feynman worked at Cornell University. There, as he recounts in this interview, Bethe was the catalyst for his ideas on resolving “the problem of the infinities.” The precise energy levels of electrons in hydrogen atoms, and the forces between the electrons (moving so rapidly that relativistic changes had to be taken into account), had already been the subject of pioneering work for three decades. Every electron, theory asserted, was surrounded by transient “virtual particles” which its mass-energy summoned up from vacuum; those particles in turn summoned up others–and the result was a mathematical cascade which predicted an infinite charge for every electron. Tomonaga had suggested a way around the problem in 1943, and his ideas became known just as Feynman at Cornell and Schwinger at Harvard were making the same crucial step. All three shared the Nobel Prize for Physics in 1965. By then, Feynman’s mathematical tools, the “Feynman integrals,” and the diagrams he had invented to trace particle interactions were part of the equipment of every theoretical physicist. Mathematician Stanislaw Ulam, another Los Alamos veteran, cites the Feynman diagrams as “a notation that can push thoughts in directions that may prove useful or even novel and decisive.” The idea of particles that travel backward in time, for example, is a natural outgrowth of that notation.
In 1950, Feynman moved to Caltech, in Pasadena. His accent is still unmistakably the transplanted New Yorker’s, but Southern California seems the appropriate habitat for him: Among the “Feynman stories” his colleagues tell, his fondness for Las Vegas and nightlife in general looms large. “My wife couldn’t believe I’d actually accept an invitation to give a speech where I’d have to wear a tuxedo,” he says. “I did change my mind a couple of times.” In the preface to The Feynman Lectures on Physics, widely used as a college text since they were collected and published in 1963, he appears with a maniacal grin, playing a conga drum. (On the bongos, it is said, he can play ten beats with one hand against eleven with the other; try it, and you may decide that quantum electrodynamics is easier.)
Among Feynman’s other achievements are his contribution to understanding the phase changes of super-cooled helium, and his work with Caltech colleague Murray Gell-Mann* on the theory of beta decay of atomic nuclei. Both subjects are still far from final resolution, he points out; indeed, he does not hesitate to call quantum electrodynamics itself a “swindle” that leaves important logical questions unanswered. What kind of man can do work of that caliber while nursing the most penetrating doubts? Read on and find out.
Omni: To someone looking at high-energy physics from the outside, its goal seems to be to find the ultimate constituents of matter. It seems a quest we can trace back to the Greeks’ atom, the “indivisible” particle. But with the big accelerators, you get fragments that are more massive than the particles you started with, and maybe quarks that can never be separated. What does that do to the quest?
Feynman: I don’t think that ever was the quest. Physicists are trying to find out how nature behaves; they may talk carelessly about some “ultimate particle” because that’s the way nature looks at a given moment, but . . . Suppose people are exploring a new continent, OK? They see water coming along the ground, they’ve seen that before, and they call it “rivers.” So they say they’re exploring to find the headwaters, they go upriver, and sure enough, there they are, it’s all going very well. But lo and behold, when they get up far enough they find the whole system’s different: There’s a great big lake, or springs, or the rivers run in a circle. You might say, “Aha! They’ve failed!” but not at all! The real reason they were doing it was to explore the land. If it turned out not to be headwaters, they might be slightly embarrassed at their carelessness in explaining themselves, but no more than that. As long as it looks like the way things are built is wheels within wheels, then you’re looking for the innermost wheel–but it might not be that way, in which case you’re looking for whatever the hell it is that you find!
Omni: But surely you must have some guess about what you’ll find; there are bound to be ridges and valleys and so on . . .?
Feynman: Yeah, but what if when you get there it’s all clouds? You can expect certain things, you can work out theorems about the topology of watersheds, but what if you find a kind of mist, maybe, with things coagulating out of it, with no way to distinguish the land from the air? The whole idea you started with is gone! That’s the kind of exciting thing that happens from time to time. One is presumptuous if one says, “We’re going to find the ultimate particle, or the unified field laws,” or “the” anything. If it turns out surprising, the scientist is even more delighted. You think he’s going to say, “Oh, it’s not like I expected, there’s no ultimate particle, I don’t want to explore it”? No, he’s going to say, “What the hell is it, then?”
Omni: You’d rather see that happen?
Feynman: Rather doesn’t make any difference: I get what I get. You can’t say it’s always going to be surprising, either; a few years ago I was very skeptical about the gauge theories,* partly because I expected the strong nuclear interaction to be more different from electrodynamics than it now looks. I was expecting mist, and now it looks like ridges and valleys after all.
Omni: Are physical theories going to keep getting more abstract and mathematical? Could there be today a theorist like Faraday in the early nineteenth century, not mathematically sophisticated but with a very powerful intuition about physics?
Feynman: I’d say the odds are strongly against it. For one thing, you need the math just to understand what’s been done so far. Beyond that, the behavior of subnuclear systems is so strange compared to the ones the brain evolved to deal with that the analysis has to be very abstract: To understand ice, you have to understand things that are themselves very unlike ice. Faraday’s models were mechanical–springs and wires and tense bands in space–and his images were from basic geometry. I think we’ve understood all we can from that point of view; what we’ve found in this century is different enough, obscure enough, that further progress will require a lot of math.
Omni: Does that limit the number of people who can contribute, or even understand what’s being done?
Feynman: Or else somebody will develop a way of thinking about the problems so that we can understand them more easily. Maybe they’ll just teach it earlier and earlier. You know, it’s not true that what is called “abstruse” math is so difficult. Take something like computer programming, and the careful logic needed for that–the kind of thinking that mama and papa would have said was only for profes
sors. Well, now it’s part of a lot of daily activities, it’s a way to make a living; their children get interested and get hold of a computer and they’re doing the most crazy, wonderful things!
Omni: . . . with ads for programming schools on every matchbook!
Feynman: Right. I don’t believe in the idea that there are a few peculiar people capable of understanding math, and the rest of the world is normal. Math is a human discovery, and it’s no more complicated than humans can understand. I had a calculus book once that said, “What one fool can do, another can.” What we’ve been able to work out about nature may look abstract and threatening to someone who hasn’t studied it, but it was fools who did it, and in the next generation, all the fools will understand it.
There’s a tendency to pomposity in all this, to make it all deep and profound. My son is taking a course in philosophy, and last night we were looking at something by Spinoza–and there was the most childish reasoning! There were all these Attributes, and Substances, all this meaningless chewing around, and we started to laugh. Now, how could we do that? Here’s this great Dutch philosopher, and we’re laughing at him. It’s because there was no excuse for it! In that same period there was Newton, there was Harvey studying the circulation of the blood, there were people with methods of analysis by which progress was being made! You can take every one of Spinoza’s propositions, and take the contrary propositions, and look at the world–and you can’t tell which is right. Sure, people were awed because he had the courage to take on these great questions, but it doesn’t do any good to have the courage if you can’t get anywhere with the question.
Omni: In your published lectures, the philosopher’s comments on science come in for some lumps . . .
Feynman: It isn’t the philosophy that gets me, it’s the pomposity. If they’d just laugh at themselves! If they’d just say, “I think it’s like this, but von Leipzig thought it was like that, and he had a good shot at it, too.” If they’d explain that this is their best guess . . . But so few of them do; instead, they seize on the possibility that there may not be any ultimate fundamental particle, and say that you should stop work and ponder with great profundity. “You haven’t thought deeply enough, first let me define the world for you.” Well, I’m going to investigate it without defining it!
Omni: How do you know which problem is the right size to attack?
Feynman: When I was in high school, I had this notion that you could take the importance of the problem and multiply by your chance of solving it. You know how a technically minded kid is, he likes the idea of optimizing everything . . . anyway, if you can get the right combination of those factors, you don’t spend your life getting nowhere with a profound problem, or solving lots of small problems that others could do just as well.
Omni: Let’s take the problem that won the Nobel Prize for you, Schwinger, and Tomonaga. Three different approaches: Was that problem especially ripe for solution?
Feynman: Well, quantum electrodynamics had been invented in the late 1920s by Dirac and others, just after quantum mechanics itself. They had it fundamentally correct, but when you went to calculate answers you ran into complicated equations that were very hard to solve. You could get a good first-order approximation, but when you tried to refine it with corrections these infinite quantities started to crop up. Everybody knew that for twenty years; it was in the back of all the books on quantum theory.
Then we got the results of experiments by Lamb* and Retherford† on the shifts in energy of the electron in hydrogen atoms. Until then, the rough prediction had been good enough, but now you had a very precise number: 1060 megacycles or whatever. And everybody said dammit, this problem has to be solved . . . they’d known the theory had problems, but now there was this very precise figure.
So Hans Bethe took this figure and made some estimates of how you could avoid the infinities by subtracting this effect from that effect, so the quantities that would tend to go to infinity were stopped short, and they’d probably stop in this order of magnitude, and he came out with something around 1000 megacycles. I remember, he’d invited a bunch of people to a party at his house, at Cornell, but he’d been called away to do some consulting. He called up during the party and told me he’d figured this out on the train. When he came back he gave a lecture on it, and showed how this cut-off procedure avoided the infinities, but was still very ad hoc and confusing. He said it would be good if someone could show how it could be cleaned up. I went up to him afterwards and said, “Oh, that’s easy, I can do that.” See, I’d started to get ideas on this when I was a senior at MIT. I’d even cooked up an answer then–wrong, of course. See, this is where Schwinger and Tomonaga and I came in, in developing a way to turn this kind of procedure into solid analysis–technically, to maintain relativistic invariance all the way through. Tomonaga had already suggested how it could be done, and at this same time Schwinger was developing his own way.
So I went to Bethe with my way of doing it. The funny thing was, I didn’t know how to do the simplest practical problems in this area–I should have learned long before, but I’d been busy playing with my own theory–so I didn’t know how to find out if my ideas worked. We did it together on the blackboard, and it was wrong. Even worse than before. I went home and thought and thought, and decided I had to learn to solve examples. So I did, and I went back to Bethe and we tried it and it worked! We’ve never been able to figure out what went wrong the first time . . . some dumb mistake.
Omni: How far had it set you back?
Feynman: Not much: maybe a month. It did me good, because I reviewed what I’d done and convinced myself that it had to work, and that these diagrams I’d invented to keep things straight were really OK.
Omni: Did you realize at that time that they’d be called “Feynman diagrams,” that they’d be in the books?
Feynman: No, not–I do remember one moment. I was in my pajamas, working on the floor with papers all around me, these funny-looking diagrams of blobs with lines sticking out. I said to myself, wouldn’t it be funny if these diagrams really are useful, and other people start using them, and Physical Review has to print these silly pictures? Of course, I couldn’t foresee–in the first place, I had no idea how many of these pictures there’d be in Physical Review, and in the second place, it never occurred to me that with everybody using them, they wouldn’t look funny anymore . . .
[At this point the interview adjourned to Professor Feynman’s office, where the tape recorder refused to start again. The cord, power switch, “record” button, all were in order; then Feynman suggested taking the tape cassette out and putting it in again.]
Feynman: There. See, you just have to know about the world. Physicists know about the world.
Omni: Take it apart and put it back together?
Feynman: Right. There’s always a little dirt, or infinity, or something.
Omni: Let’s follow that up. In your lectures, you say that our physical theories do well at uniting various classes of phenomena, and then X-rays or mesons or the like show up; “There are always many threads hanging out in all directions.” What are some of the loose threads you see in physics today?
Feynman: Well, there are the masses of the particles: The gauge theories give beautiful patterns for the interactions, but not for the masses, and we need to understand this irregular set of numbers. In the strong nuclear interaction, we have this theory of colored* quarks and gluons, very precise and completely stated, but with very few hard predictions. It’s technically very difficult to get a sharp test of the theory, and that’s a challenge. I feel passionately that that’s a loose thread; while there’s no evidence in conflict with the theory, we’re not likely to make much progress until we can check hard predictions with hard numbers.
Omni: What about cosmology? Dirac’s suggestion that the fundamental constants change with time, or the idea that physical law was different at the instant of the Big Bang?
Feynman: That would open up a lot of questions. So far
, physics has tried to find laws and constants without asking where they came from, but we may be approaching the point where we’ll be forced to consider history.
Omni: Do you have any guesses on that?
Feynman: No.
Omni: None at all? No leaning either way?
Feynman: No, really. That’s the way I am about almost everything. Earlier, you didn’t ask whether I thought that there’s a fundamental particle, or whether it’s all mist; I would have told you that I haven’t the slightest idea. Now, in order to work hard on something, you have to get yourself believing that the answer’s over there, so you’ll dig hard there, right? So you temporarily prejudice or predispose yourself–but all the time, in the back of your mind, you’re laughing. Forget what you hear about science without prejudice. Here, in an interview, talking about the Big Bang, I have no prejudices–but when I’m working, I have a lot of them.
Omni: Prejudices in favor of . . . what? Symmetry, simplicity . . .?
Feynman: In favor of my mood of the day. One day I’ll be convinced there’s a certain type of symmetry that everybody believes in, the next day I’ll try to figure out the consequences if it’s not, and everybody’s crazy but me. But the thing that’s unusual about good scientists is that while they’re doing whatever they’re doing, they’re not so sure of themselves as others usually are. They can live with steady doubt, think “maybe it’s so” and act on that, all the time knowing it’s only “maybe.” Many people find that difficult; they think it means detachment or coldness. It’s not coldness! It’s a much deeper and warmer understanding, and it means you can be digging somewhere where you’re temporarily convinced you’ll find the answer, and somebody comes up and says, “Have you seen what they’re coming up with over there?”, and you look up and say “Jeez! I’m in the wrong place!” It happens all the time.
The Pleasure of Finding Things Out Page 19
