Linus Pauling Interview, July 27, 1990

LINUS PAULING: -tend to be more complicated and of such a nature that, for the most part, you can't find a rigorously correct answer. You have to be satisfied with approximations. And you may have, and usually do have, to attack these problems in a semi-empirical, semi-theoretical way. Physicists-a very active field in physics is particle physics. Here, again, they don't know exactly what they're doing. But they make an effort to carry out arguments in a quite rigorous way, and I never have been very interested in rigor.

Mathematics... When I was a graduate student taking a course from E.T. Bell, a 00:01:00famous number theory mathematician, he suggested that I become a mathematician, and in particular that I perhaps do some work or write a thesis on a Fibonacci series of numbers. I'm interested in them now. Well, I worked a little while on a Fibonacci series, or number theory, and never could get very interested in it. Mathematicians are logicians. They try to develop completely logical arguments the way Whitehead and Russell did in Principia Mathematica of formulating a few 00:02:00postulates and then driving the whole of mathematics from these postulates. Mathematicians try to prove something rigorously. And I suppose that their main emphasis is on logic and rigor, rather than on solving problems relating, in any other way than the fact that mathematics is a part of the world, to the general problem of the structure of the universe. I think all of my life, I've been interested in the structure of the universe, in a sense, and have been attempting to formulate a basic set of principles about the nature of the universe.

I read scientific papers quite a lot and read about scientific discoveries, and of course every day perhaps, or every few days, there's something new to me that I read. When I read about an idea that is new to me, I ask is this compatible with the picture that I have of the universe as a whole, or is it not? And if it is not, I ask why. Is there something- here seems to be something that I don't understand, so perhaps I ought to work on it. So, I pile up problems that puzzle 00:04:00me, that I should like to work on.

THOMAS HAGER: You have made advances throughout your career in forming those principles and elucidating basic ideas about structure, especially about structural problems. Where do you think your most important contribution lies, out of all the work that you've done? Now, I've read before that you considered your work on the chemical bond, out of all your accomplishments, the single most important. Is that still the way you feel?

LP: Well, I suppose so. It's hard to compare work of that sort with other things that I have done. But if I ask what about the effect of my work on the nature of the chemical bond, since the 1930s when that work was published, the whole 00:05:00science of chemistry has changed. People say - used to say - modern chemistry began with Lavoisier [?] in 1890, '91. And in a sense, it did, except one could now say very modern chemistry began in the 1930s, essentially with my work, although I wasn't the only person involved.

I was in an unusual position in the 1920s, 1925, '26. I had a great background of knowledge of chemistry, empirical chemistry. There were a great many questions that I could ask about chemistry at that time and didn't know the 00:06:00answers. I also had a quite good background of knowledge of physics, theoretical physics, and mathematics. And I don't think there was anybody else in the world who had the same combination of extensive knowledge of chemistry, the facts of chemistry and what theories existed, and this knowledge of theoretical physics and mathematics. So, I was in a position to make rapid progress in the 1930s, 1927 on. 1926, actually. The same year in which quantum mechanics was discovered, I wrote my first paper, the first paper ever published that was significant on the structure of atoms with more than one electron. It was called 00:07:00"Die Abschirmungskonstanten der relativistischen oder magnetischen Röntgen dublettan," [sic, Röntgenstrahlendubletts] and I applied a quantum mechanical method to this problem. And of course, then following years that was what I did. If I hadn't done it, there might have been a delay of 10 years perhaps before anybody did anything similar, or 20 years, even.

TH: Yeah.

LP: I said, in my paper in 1927 - or '28, I'm not sure which year - in PNAS on the nature of the chemical bond that I found that the resonance theory of quantum mechanics explains the tetrahedral arrangement of the four bonds of 00:08:00carbon. And here I didn't get that published until 1931. March of 1931. I felt that I had found that the equations were so complicated - I said also I'll publish details later - equations were so complicated that I never could be sure that I could present the arguments in such a way that they would be convincing to anybody. And so, it took me four years to find a way of handling the quantum mechanical problem that I felt had to be convincing. And that was in my first 1931 paper.

TH: Yeah.

LP: And in it, I was able to provide answers to a half a dozen different puzzling questions in chemistry that I hadn't known the answers to before, and that no one had known the answers to before.

Well, what about the bomb test treaty? How important-first, how important was the bomb test treaty, but how important was I in relation to the bomb test treaty? Gunnar Jahn, the chairman of the Nobel Committee said that if there hadn't been someone like me agitating about it, probably the bomb test treaty would not have been made. And I have argued that the bomb test treaty has saved 00:10:00millions of unborn children from having gross physical or mental defect, and millions of people now living, or living in the future, from dying of cancer. And probably tens of millions, in fact, in each category.

The Chernobyl disaster was pretty bad because it perhaps means a million defective children and a million people with cancer. I was just reading this morning about the disaster relief efforts of the Soviet Union moving hundreds of thousands of people out of-well, they're just doing this four years later. They've been exposed to this radioactivity in and of perhaps 100,000 square 00:11:00miles. Several- a tremendous area contaminated with radioactive fallout.

TH: Let me check one thing with you. And I know we're going overtime here, and I want to-

LP: And then there's the vitamin C matter. I argue- in this book I shall argue that if people will make proper use of vitamins, and especially- well, both for prophylactic purposes against cancer, and therapeutic purposes when cancer has developed, hundreds of thousands of people a year in the United States, 100,000 or 200,000 probably could have their lives saved. And in the world, many more. So, how important is that? And I think because of my reputation, if this comes 00:12:00about, I will have a good bit of responsibility for its coming about.

TH: The bomb test treaty, vitamin C, the nature of the chemical bond, those three things then.

LP: Yes. Of course, there are several things that I did to initiate the field of molecular biology and molecular medicine.

TH: Sure, sure. That sickle cell anemia work and...

LP: Yes, that was molecular medicine. The structure, the secondary structure of proteins, and of course agitation, stimulation of Watson and Crick, too. So, to 00:13:00have taken an important part in starting the development of the field of molecular biology and of molecular medicine is a fourth contribution.

TH: Yeah, well, believe [laughs], when I think of working with all of this material, and plus all of the other stuff in addition to those four major areas, it's amazing. I just want to check one thing with you and then we'll end this. Your working style in questions relating to structural chemistry especially has been summarized, and I just want to see if you agree with this. You have an approach in which you use the data that you have looked at, or data that you've 00:14:00gathered yourself, to sort of make a preliminary leap of understanding about a program. Let's say, for instance, the question of the tetrahedral binding of carbon where you said that you had an understanding of how resonance worked in that structure, but it took you four years to work out all the mathematics to convince people that that was correct. So, you have a leap of understanding-

LP: Yeah, I'm not sure that's a good example of a leap of understanding. Here, I knew that a carbon atom that forms four single bonds directs them to the corners of a regular tetrahedron. I knew already, in 1927 or '28, that - and everybody 00:15:00accepted that already - perhaps not everybody - that quantum mechanics was essentially correct, so far as chemistry goes. Molecular structure. Therefore, quantum mechanics must be responsible for [laughs] the tetrahedral carbon atom. So, that's such a simple argument, it's hardly a leap of understanding.

And so, I just had the problem of understanding the quantum mechanical equations well enough to see why quantum mechanics required the tetrahedral carbon atom. And it was complicated enough. The mathematics was complicated enough. So, it took me four years until the end of 1930, beginning of '31, to be able to present the theory in a way that people could accept it. And of course, it soon 00:16:00got into the freshmen texts and the high school texts, too.

But in other cases, there has been a leap. A discontinuity in understanding. All physicians knew about sickle cell anemia. Many biochemists knew about it. So, when I began thinking about it, immediately I had the idea, and it was a logical one. If the red cells are sickled in the venous blood but not sickled in the arterial blood, something is responsible. And the substance present in largest amount is hemoglobin, so likely the hemoglobin is responsible, and it's 00:17:00different in that it's oxygenated when it goes from- So, immediately I formulated this picture of the process. And of course, it took some time to carry out the experiments to prove it, but it was right. Many times, I have had ideas of that sort. My theory of anesthesia; I puzzled over the fact that xenon is a good general anesthetic agent. I couldn't see why because it doesn't have any chemical property.

TH: Right, a noble gas.

LP: And eight years, seven years later, it took me seven years of thinking about that problem from time to time. Seven years later, I'd suddenly said I understand anesthesia. So, many times in my work - and of course there are minor 00:18:00discoveries that I've made in a similar way - many times there is this leap, quantum leap in understanding. As I say, I don't think the tetrahedral carbon atom is a good example because anybody could see that quantum mechanics must lead to the tetrahedral carbon atom, because we have it. It's like these fellows who do quantum mechanics of molecules or of nuclei. You have some experimental data. They set up the Schrödinger equation in the computer and put the interaction, function in, and the computer brings out a set of energy values which agree with the experiment. And they say fine, so we understand these energy levels. Well, they don't understand them. They just know, and anybody could predict, that if you make quantum mechanical calculations that are 00:19:00accurate, they'll agree with the experiment.

TH: [Laughs].

LP: There's no evidence that quantum mechanics doesn't work. So, they haven't discovered anything, really. They don't understand. And they don't understand why I ask them, "Do you understand?" and I'm not satisfied when they say "Yes, we've carried out the quantum mechanical calculations and they agree with the experiment." And I say, "That's not understanding. You have to have some feeling as to why the computer gave the right answer and why the experimental values are what they are."

TH: Mm-hmm. It's interesting that you called it a quantum leap of understanding in other applications, that sort of-

LP: Well, it's not original with me, this expression. Other people have used it. 00:20:00Quantum is a part of the language of the layman now.

TH: Yeah. But is that, do you feel it's an accurate description of that process?

LP: Yes. Well, there was a professor of physical chemistry at Cornell, Wilder D. Bancroft, who was interested in quantum leaps and understanding, but he called them hunches.

TH: [Laughs].

LP: And he asked 100 chemists about their having hunches, and he said there were a half a dozen who seemed not to know what he was talking about. But many others did have hunches. He was interested in just that question, how many people have these quantum leaps in understanding. This was- he could have- this was about 1929 I think, a paper in Proceedings of the National Academy of Sciences by 00:21:00Wilder D. Bancroft.

TH: Well, the question is why are your quantum leaps so much better than most peoples'?

LP: Okay. And my usual answer is that I'm not the smartest man in the world, by any means. A good memory, and where the difference is that I think more about these matters than other people. Than other scientists, even. And, as I said to David Harker when he asked the question about 1935, when he said, "How do you go about having new ideas, Dr. Pauling?" Or good new ideas, I guess he said. Good new ideas. And I said, "Well, you have a lot of ideas and throw away the bad ones."

TH: [Laughs].

LP: And so, I have developed the ability, I think, to decide on whether an idea is a good one in the sense that there's some chance of applying it and solving a problem in a reasonable period of time, such as 10 years. I worked for 11 years on the problem of the way in which polypeptide chains are folded in proteins before I discovered the alpha helix and the pleated sheets. And for seven years thinking about anesthesia, and for four years on that - or perhaps five years, 00:23:00because I had started right away in 1926 - on the chemical bond problem, the tetrahedral carbon atom. Heitler and London, on the one hand, and Ed Condon on the other, had made important contributions about the chemical bond in H2, and they and others were trying to extend these ideas to complicated molecules, but they didn't make much practical progress, I would say. It wasn't until my 1931 paper and the others came along that a really good quantum mechanical picture of molecules came into existence.

About 1933 or four, I gave up the idea of making- myself making very complicated quantum mechanical calculations about molecular structure, for the reasons that I've mentioned. But I made a lot of simple quantum mechanical calculations and drew conclusions from them, and I realized that if you could ever make really accurate quantum mechanical calculations, you wouldn't learn anything from them because they would just agree with the experiment.

TH: Well, that freed you up to spend your time on more productive work.

LP: Yes.

TH: Listen, I don't want to take any longer. I don't want to get your throat sore here or anything like that. So, we can end this today. There's so much 00:25:00m-[tape ends].