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Oral History Transcript — Sir Denys Wilkinson

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Interview with Sir Denys Wilkinson
By C. J. Meyers
At Oxford University
1964

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Denys Wilkinson; 1964

ABSTRACT: Administrative work at Oxford; research at Brookhaven National. Lab; importance of family life; interest in ornithology, medieval architecture; approach to physics problems; self-taught in nuclear physics; importance in "imagined criticism from real colleagues; new ideas do not end at age twenty-five; role of conferences and holidays in generating ideas; chance observations and the prepared mind; discovering laws of physics; influence of computers; "accidental II selection of research problems; roles of colleagues in testing new ideas and response to criticism; personal life (non-compartmentalization of life), absence of scientific heroes (except Eugene Wigner). Also prominently mentioned are: Brookhaven National Laboratory, and University of Cambridge.

Transcript

The conversation began by the interviewer making a reference to a joke on the wall, a cartoon about a stag being held at bay by wolves.

Wilkinson:

There is very great feeling behind that. Maybe you caught snippets of the conversation when I was at the door; almost all my life is spent not doing physics — which is the popular misconception of what the head of a physics department does — but in enabling other people to do their physics. That if you like is my job now. When I first came here in 1957, it was to an ad hominem professorship which in principle would have allowed me to go on as. I had been doing in Cambridge, running a small group, but it turned out that that wasn't the most efficient way of getting as much physics done as I felt I could get done. I regarded my function in this as being responsible for the total output of a. group, rather than my personal output. It seemed as though there was some more organization needed and so I built up the nuclear physics strength at Oxford. But at the same time I began to do all my personal work with my own hands in nuclear physics in America. I do still regard myself primarily as a physicist and I bitterly grudge the time I spend in doing other things. I've got a curious modus vivendi in that I don't try to do experimental work in this country: I go to America every summer for two months, to Brookhaven, and I go two or three or four times a year in addition for periods of usually between a week and two weeks. There's a group of chaps I work with at Brookhaven, I have a permanent desk there, I even have a car there and I have an apartment permanently available. I don't actually rent it continuously but it is always available to me. So it's easy to slip over to Brookhaven. In twelve hours I'm there and in the laboratory. And in that way I get almost completely away from the paper and the hounds, and I am relatively undisturbed. What I do in this country in the physics line is think, as and when I can; of course I stay in very close touch with the work of the laboratory in the sense that in my work I talk with a lot of people and I hope to exert a seminal influence or whatever you like to call it. But I don't regard that as my own work. I don't put my name on experimental papers that come out of this laboratory, unless I chance actually to have found the time for a personal involvement, which is very rare.

Meyers:

Do superior facilities exert any influence in drawing you to America?

Wilkinson:

No, it's not so much the facilities. Comparable and in some ways superior facilities are available down the road at Harwell and at the Rutherford Laboratory and here in this laboratory. No the thing is time and freedom from interruption. You see we still run a kind of old-fashioned Jehova (?) system in physics departments in this country where there is the head of the department and so almost everything gets referred to him by the central offices. So every day I have somewhere between a minimum of three to a maximum of a dozen or so communications from the Registry, and at least I have to slit the envelopes open and see what's inside them. And if for example, I were trying to work out at Harwell and the Vice-Chancellor or the Registrar or the Finance Committee or the General Board or someone else wanted to grill me, well I would be available at Harwell; I would have to come back here because I am the head of the department and that is my responsibility. But if I am in Brookhaven I can't be gotten hold of so readily. So it's a sort of piece of insulation between me and the grinding machine. There, in many ways superior facilities in the States but I think in my field the superiority is more in attitude of mind and general intellectual climate. Now I'm obviously not helping those things here by going away to the States; on the other hand by going away to the States I do keep myself in the mainstream of research which otherwise I would not be able to do. This isn't just a personal matter: all you have to do is look around at the experimental nuclear physicists who are heads of departments in this country, and not a single one is doing scientific research with his own hands. There are many of them, and they've all packed in; and I would agree that I've packed in in the same sense as far as my research in this country goes. They probably exert the same kind of influence on the people in their departments that I try to do but there is none of them publishing under his own name. (There are I suppose one or two exceptions, but one knows them and one knows the kind of thing they do and it's not the kind of thing I would like to do myself.) So it's the system that grinds one down and nobody recognizes what he lets himself in for. As I say my own solution is an unusual one. I am fortunate in being able to adopt it, but of course it is not everybody's meat. You see I have no summer holiday; I haven't had one for twelve years. My colleagues see me go off to the Long Island beaches; they say how wonderful it is to have two months holiday on American beaches every year. But it isn't that; I don't take a holiday then, I don't see much of the beaches.

Meyers:

Do you take any holidays?

Wilkinson:

Yes, we — I have a wife and three children — and for many years now, at least since I started this commuting in 1954, we've had our big family holiday at Easter time and we always, unless something unusual prevents it, go away for about two weeks — last year we went away for five weeks, the really big family holiday of our lifetime so far, but we make a big point of always getting away. Then we always go away for a few days to my parents at Christmas time which is another fixed period of relaxation. I try to get away during the year with my wife for a couple of days or so in addition to the family holiday. Then about every other year the family comes with me to the States for the summer. But I enjoy holidays enormously. I don't in any way grudge the time. I wish I took more. But on the argument that a change is as good as a rest, going to Brookhaven is refreshing for me. I feel a quite different person there, I feel myself under a different set of pressures and that's good. But I also do value proper holidays. In the course of physics I do take a number of trips to other countries and I like travel. One of my biggest interests outside of physics is medieval architecture and that's one reason why I'm very keen on travelling particularly to European countries. For example, in February I went to Georgia in the Caucasus for what was nominally a conference, but in Georgia and in Armenia you find some particularly interesting Romanesque churches of a type which you don't find anywhere else. So that sort of thing is very exciting. And the other sort of thing that I'm interested in outside of physics is birds. I do almost no bird watching in this country anymore, but when I go away into a new crop of birds, I get extremely excited and spend as much time as I can on that.

Meyers:

How did you get interested in bird-watching?

Wilkinson:

Well, really in two ways. I always had a little bit of interest in birds. When I went to the seaside — gulls and things of that sort — I would get a little book and identify them. But during the war I was in the atomic weapons project and my job was measuring fast neutron fluxes and so day after day I was exposed to neutrons. I obviously got too many because, I think it was in 1947, I got radiation sickness quite badly. In fact I was despaired of; I was given six months to live by the Regius Professor of Medicine at Cambridge. As it turned out I was perfectly all right again in 18 months, but for a time afterwards it looked as if I probably would not be able to go back to nuclear physics. At the time a number of theories of bird navigation of a physical character were being put on the market, and my oId tutor at my Cambridge college, W. H. Thorpe, an animal behaviorist and a person who interests himself very seriously in the careers of the people he has had to deal with, interested me in these. I actually did one piece of work which was I think fairly valuable. Before the war the old style of bird navigation experiment was to take a very' large number of birds from their nests and simply displace them to a big distance somewhere between fifty and perhaps a thousand miles and let them go and see when they got back to their nests. And then you tried to look for evidence of a general navigational ability in the rate at which they returned home. An interesting feature was that they get home very slowly, about as many miles in a day as they are capable of flying in an hour on the average, and with a very wide distribution in time. And with small birds most of them don't get home. And this is just the behavior you would expect if in fact they were searching randomly for home, as it were diffusing; if you imagine a gas of birds diffused throughout the continent, obviously after a certain length of time they give up or they are eaten or something. So I simply calculated, using the usual diffusion equation, in fact — using my experience of thermal neutrons during the war, what sort of distribution in time you would expect from random search. And it turned out that one can in fact fit the results as accurately as you like with such a random hypothesis. And I was extremely careful to say that this does not prove that they are searching randomly. What I did say was that one could not obtain evidence of non-randomness of behavior from the sort of experiment as then practiced. What one must do is look for explicit non-randomness in the behavior, during the time when you have got them under your observation, after their release. So this led us to suggest experiments, in which birds were released singly and followed with binoculars for as long as possible. The behavior of the group was then analyzed on the basis of this individual non-correlated behavior. In other words, look for non-randomness in the direction in which the group of birds disappears even though the group is made up of uncorrelated individuals. So in this period I actually went into partnership with one of Thorpeís Ph.D. pupils, G.V.T. Matthews, and we did quite a lot of bird navigation experiments together. Then at the end of it my blood got better and I was pronounced safe to go back into low radiation levels. I had a choice - would I stick with my new interests or go back into physics — and I went back into physics.

Meyers:

So you left animal behavior as a hobby?

Wilkinson:

I left it as a hobby. I've done a little bit since then, I keep in close touch with the literature, and I generally act as sort of devil's advocate if new physical navigation theories come along.

Meyers:

Do you see any other parallels between your work in animal behavior and in physics? I see you were applying physical methods to the new field.

Wilkinson:

Just because I knew physics, you see, obviously. I often wonder now when I see a certain pattern of behavior, if one could make a model of this. But these are little idle speculations, rather than the urge to go out and try and apply physics to biological problems. Pm sure one can and I do have friends and colleagues who are physical biologists. But Iím not sure of the deep significance of many of the things that have come out of applying physics to these gross anatomical types of biology. For instance we now understand a lot about the flight of birds and insects and so on. Well, all right, we understand how they fly. That doesn't take us any further forward. It doesn't seem to get anywhere. I mean you can understand why you don't have birds with wing spans of fifty feet; you know the wings would come off. The strength of materials is interesting, but I don't get very excited about it. And then there are one or two problems that one thinks one can calculate and where the answer contradicts the facts. For example, the migration of the ruby throated hummingbird across the Gulf of Mexico. It seems to be established that the bird can fly straight across the Gulf. You know the humming-bird's mass, the rate of metabolism, you know how much energy it costs to keep the thing in the air, and it isn't big enough, I mean it can't take on enough food to make it. So you can prove if you like that it can't fly across the Gulf. Now either this means that it doesn't fly across the Gulf and there's a little bit of doubt about this still or obviously there is something wrong with the calculation. So this might be interesting. I suppose if one was really forced into this contradiction, you would have to find out what changes there are in humming-birds' metabolic process or something which enable them to do this. But there again this seems to me to be a little problem, a small problem.

Meyers:

Once you get out of physics the problems you work on do not link up with other problems so nicely.

Wilkinson:

Yes, I suppose in a sense that is a definition of the division between the sciences. The divisions naturally form themselves in those places where one's leads don't link across.

Meyers:

You have the college system here where you have your meals at least in a mixed group.

Wilkinson:

Yes, that's right

Meyers:

Do you find in this situation that you gravitate towards scientists other than physicists?

Wilkinson:

I tend to regard college as a non-scientific place. There are other scientists in my college and I don't avoid them, but I would sooner talk to a historian or a classicist or something just for the change. And I very much enjoy eating at college. I think I should also emphasize that. I like conversation of a general character, and it's a wonderful place for it, partly because it is this great hotch potch of different disciplines. Well, let's look at the questions "How do you organize your time?" Well, you see... I imagine that these questions refer to science.

Meyers:

(Yes) If there is a difference, and there probably is, between the way you organize things now and the way you organized them when you were younger, we could go into that.

Wilkinson:

Yes, well when I was younger I used to spend most of my time on physics. I think there is not a very great deal of difference between the way I work now when I'm in Brookhaven and the way I used to work except of course, since my year is broken up in this way, I tend to try to find problems which I can either do in a couple of months or the kind which are not hurt by being left for a couple of months. So I try to avoid the kind of experiments which turn into programs of measurement. I came out of the war with two obsessions: one was that I wanted to work on 'simple' problems, that is to say simple systems. During the war we had been trying to make uranium go 'bang', and that is an exceedingly complex problem, which one doesn't understand in any sort of fundamental terms, but in highly empirical terms.

Meyers:

When you say 'simple' you mean going back to first principles?

Wilkinson:

That's right. I came out wanting to handle systems — nuclei — which were as simple as possible, had as few particles as possible, which gave some hope of being understandable if not from first principles at least on the basis of a model which would itself be directly relatable to first principles. So that was one thing. And it was almost an obsession because during the war I had to keep away from academic problems. In the course of the uranium business quite a number of interesting sidelines opened themselves up and I would have liked to have plunged down them. But I couldn't, and it was frustrating. The other thing which came out of the war work was an obsession with a technicality. Almost everything one does in nuclear physics turns into analyzing the distribution of a sequence of impulses. The information comes to you out of your apparatus in analogue form, electrical pulses of various heights, and you want to turn it into digital information. During the war one first recognized the need for this and extremely complex and cumbersome devices were built for doing this job. I felt that there should be a simple and good way of doing this, and that also was an obsession, to find a way of doing it. And I did in fact find it and this is now the basis of certainly 95% of all instruments in the world which do the job. But I hit upon what is universally recognized as the right way to do this job. Well, that was really on the one hand an obsession. I had to find the right way to do this and on the other hand I needed to find how to do it for the work which I embarked on in nuclear physics. So the two needs converged. The actual problem I worked on was the photo-disintegration of the deuteron. The deuteron is the simplest nucleus, which satisfied my simplicity criterion. The photon is the simplest particle, the quantum of electro-magnetic field; we think we understand that pretty well completely. So putting the simplest projectile into the simplest nucleus was the simplest thing that I could think of doing. And there were at that time a number of fairly basic questions that could be answered by this kind of experiment. On the other hand it was a very tough and a lengthy business, and took about six years. During this time I did do some other things, but this was my chief work. And similarly the invention, if you like to use that vulgar term, and development of this pulse height analysis method also took several years.

Meyers:

When you went about following these problems up, did you have to present — a program to whatever organization supplied the money?

Wilkinson:

Not really. The organization, the Cavendish, was very loose. I simply said to Frisch, who had come to Cambridge shortly after the war, "I'm interested in photodisintegration of the deuteron", and he said, "Oh that's fine, that seems a sensible thing to work on". So I worked on it. It wasnít very costly, only a few thousand pounds I suppose, though I think of it more in terms of hundreds. Of course nowadays it would be much more, because you would do it in a different way. And three graduate students got involved in this, and those were spacious days. The curious thing is that if I look back to what has happened to physics since I went into it (in 1943 in the middle of the war) the further I look back the more spacious it seems to be. One might think that in war time the pressure would be enormous and that one would just work at fever pitch the whole time but it doesn't seem to be like that. I mean I remember that we used to go out of the laboratory at tea time, go down to Joe Lyons or down to a British Restaurant type of place, a group of us, technicians and everybody combined, and take about an hour at tea and maybe go to a book shop afterwards on the way back and so on. Holidays I seem to remember were longer and I felt freer. This I don't really understand. Then when I came out and started this purely academic business, I didn't feel under any pressure. I mean I knew that other people in the world were interested in this, but I was interested in finding out what I thought the right answer was and was not really stimulated or very much affected by the fact that other people were doing it. It certainly didn't strike me as a race. Devising this pulse height analyzer again was a completely personal matter with me. I mean I knew that it would be useful if it worked. I didn't patent it and it's a multimillion dollar industry today this thing and I presumably could have done pretty well. But I had no interest in that kind of thing. I didn't feel under any particular pressures at all, but then as time has gone on the pressures have built up. I don't feel very pressured in work; in fact I often let things go several years without publishing them. If I know that something is hot and of value to the community, then I publish it straight away. If either a possible excitement that might have been hasn't materialized, or it just turns out to be a humdrum measurement that anybody could do and that isn't particularly needed then I'll put it on one side. I don't publish for the sake of publication.

Meyers:

We'll probably come back to this again. But I asked the question because I was wondering not about pressures to publish after the work was done but what kind of restrictions were placed on you before you did the work, or how well thought out it had to be before it was done.

Wilkinson:

Well I think that the only restrictions that (have felt on my work the whole time has been facilities and financial restrictions and of course one's own abilities obviously are a restriction. I've never worked under direction actually, this has been partly good luck and partly bad. During the war I was under direction when I started, but quite quickly the senior people left Cambridge and I was left behind with a very young group, without any close direction (there was a senior person there but in fact he didn't take very much interest in what we were doing).

Meyers:

You were young yourself then.

Wilkinson:

Yes, in fact I was 21 in 1943. We even wrote a report in which we thanked this chap for not making any suggestion during the course of this work. I mean that was the sort of the degree to which he involved himself in it.

Meyers:

Is this being sarcastic?

Wilkinson:

Yes it was. He was a frightful nuisance. He used to correct the grammar, but not interest himself very much in the physics. So I had a program of measurements, I was told, 'measure these cross-sections, develop a method of measuring fast neutron flux'. I wasn't even told along what lines to move. This was good because it enabled me to develop my own initiative, my own ideas, but it was learning to swim by being thrown into the deep end. I didn't have a mentor to whom I could go. I regard myself as self-taught from the point of view of nuclear physics. I never worked as a junior member of a group except during the first three or four months of my research at Cambridge. I've always been either equal partner or the boss of the outfit so to speak. I'm sure that that is both good and bad. I often feel that it would have been good for me if I had learned one senior man's way of thinking and going about business. I think this might have been useful because if you do know how somebody else would have thought about the problem you can always think about it two ways, your own and what you know somebody else's way would have been. I do in fact make conscious efforts along those lines. I come to a conclusion then I say now so and so, what is he going to say about this, and I imagine him then tearing my work to pieces to the best of his ability and this gives me a number of questions to answer.

Meyers:

Do you have a few special people who go into this gallery of critics?

Wilkinson:

Yes, I think I do. Of course they're different people for different sorts of work. I work in a very restricted way in that I interest myself chiefly in the very light nuclei, up to about neon or so, I mean I know a certain amount about the heavier ones but I never actually worked with them very much, a little bit. But in another sense I work very widely in that I interest myself in all conceivable aspects of the properties of the light nuclei. I know these few light nuclei by their first names, and have an extreme feeling of familiarity with them. I watched them grow up, you see. If you look at the level schemes as published shortly after the war, there was nothing there. It was known that lithium 7, lithium 6 existed, it was just beginning to be known that they had an excited state, and there was a little confusion about that. Many of the nuclei of mass less than 20 of course had not been discovered then in fact there are several just waiting to be discovered. I discovered several myself. I heard of a new one only last week, nitrogen 18, which had been thought to be either just stable or just unstable, it's one of those which is touch and go. And well it's like getting a new member of the family. So I found a lot of satisfaction that way in knowing more or less everything there was to be known about a restricted number of nuclei. But in addition to this (I'm an experimenter but I have strong theoretical interests too) I have made one or two semi-quantitative 'theoretical contributions, particularly in the field of photonuclear physics which is something which does stretch throughout the periodic table, so my theoretical interests extend into other channels, but my own experimental involvement has been in this rather restricted group. We were talking about the way in which I imagine criticism. I go to different people for this imagined criticism depending on the sort of problem I'm working on. I have a colleague in Brookhaven, Dave Alburger, who is a real perfectionist in his measurements, and if I make a measurement in which I base a conclusion on two numbers being different, and if they differ by two and a half standard deviations I imagine him saying, 'Well, that only gives you a ten to one chance.' So that's one way in which I use imagined criticism, in determining whether the problem has been done well enough. . Then in my theoretical interests, I have a number of theoreticians who I imagine saying to me "Oh yes well you know you've missed out this and you've missed out that. You just can't rely on this result unless you put in this and that." Well, I don't have the time or the ability to put in this and that, I mean it becomes a real professional theoretician's job to put in this and that, and I have to decide whether I consider that it is valuable without putting in this and that or whether I should go into collaboration with some proper theoretician who would be able to do it for me. Well — and so it goes on. There's a man — Gerry Brown — who has just gone back to the States, and he is a theoretician and a very outspoken critic, and I can always imagine his outspokenness if I find myself doing something a bit too sloppy. I'm a very sloppy theoretician. Of course I'm not really a theoretician at all but there are a number of problems, and I've been lucky in hitting on a few of them, which you can sketch out using sloppy techniques. I think if I've got a forte, it is in being able to recognize what problems I can handle. I've not since the early days gone in for program of measurement. You could see a number of programs in my work but only by connecting together separated experiments. I mean there are programs which are only programs in retrospect, they were not planned as programs. For example I've done quite a lot of work on beta emission from neutron-rich light nuclei. And if you put together my papers on such, they look like a program. It seems that this man said that he's going to interest himself in the neutron-rich light nuclei and has worked through them. But that's false. I haven't come to it like that. I've come to it in a quite different way, either by accident or by being interested in the properties of a particular state that could be reached by beta emission from such a nucleus. And because I wanted to make this state, I had to make all the other states that it chances to lead to at the same time, so I've had to study the whole beta emission in order to get out this one piece of information. Then I tied the whole thing up and made it into a study in its own right, so I think there has been more of that retrospective programming, than any deliberate planning. I'm interested in doing experiments to answer specific questions. I'm not interested in amassing data. I think that if there is a characteristic about my work it is that, which I am not constitutionally well adapted to simply assembling large amounts of experimental material, the 'botanical' type of investigation — you know, like going out and naming flowers and things of that sort. I recognize the value of this — and I used to turn my nose up at it a little bit, particularly at beta ray spectroscopists who would just examine one beta emitter after another and make accurate measurements and then publish it and then go on to the next one. I couldn't see the point in doing this. It was just gathering uninterpretable data ad infinitum, wherever you happened to find it. Well, then suddenly the hypothesis of their model came along, and this beta ray, spectroscopy data was its chief quarry; and it could not have been done but for these chaps who for years and years had been, as I had thought, unprofitably simply measuring things. So it was really quite a shock because it showed me that something really big could come out of apparently useless measurements. Of course not one of these people would have claimed at the time that he was measuring it in order to enable such an interpretation. That was the way things turned out. But that hasn't made me want to do that kind of work myself. I've always wanted to experiment in order to answer a question.

Meyers:

It sounds like more of a temperamental thing.

Wilkinson:

It's a temperamental thing, but it has been a very important thing with me. And that brings us back to another question to do with my present activities: you see the head of a department can't afford to run it according to his own prejudices, to his own whims and way of work. I couldn't have everybody in the department adopting this same attitude. In a department there must be a background of work going on of a program character, just to give the thing a continuing frame of reference. And the problems that I consider as being really interesting will then arise out of this background of work from time to time. And that I think is the way in which big discoveries are made. Most of them in nuclear physics have been made accidentally or quasi-accidentally, many of them in the process of what I would consider a rather humdrum series of measurements. So one can't run a department, particularly a big one like this, on the basis of a whole mass of individuals in an uncorrelated way doing things which interest them and which may not interest anybody else.

Meyers:

You don't think it could work itself out?

Wilkinson:

No. I think it would be chaos. I don't believe one could build up a department on this basis. I've seen this happen with two people, both of whom I admire enormously and who are absolutely top rate physicists. They themselves had an exceedingly high standard of what they would allow themselves to be interested in. So they were both unable to express interest in what I might call the work of a program type, a straightforward valuable PhD thesis. And so their departments dwindled because they just weren't able to force themselves to involve themselves in things that didn't match up to their own intellectual standards. And obviously if you have a large department there are going to be all types, and presumably the majority of them are of the average intellectual standard and not a very high one. If you impose a very high intellectual standard before you pay any attention to what they're doing, then the department can't run as a department.

Meyers:

The question of periods of differing activity?

Wilkinson:

I think in fact we did effectively talk about this question of periods or cycles in that I explained that there had been quite a. big period early on when I worked on a very simple but technically difficult problem that lasted several years, and since then. Oh, oh, I'm talking now about the actual way in which the work has gone, not whether there have been periods which have been especially creative. Is that what we're supposed to be talking about?

Meyers:

Well, it could be either. We're interested in both.

Wilkinson:

Well I'll answer the first one first. There have indeed been cycles of different sorts of interest, and as I think I've already explained it's been really a question of parallel threads of interest. That is to say that over a period of about ten years, I may have been interested in three or four different problems, and worked on them either all simultaneously or a month or two on one, and a month or two on the other. So they're not so much short periods of a year or two on one problem and then another year or two on another problem. I rather worked in a parallel fashion on a number of problems. And that I still tend to do. Now, as for particularly creative periods, it's very difficult to say, isn't it, oneself, because oneís own estimate of ones work may not be the same as the world of science's judgment. I suppose that now that this gigantic annual index of references is coming out you can do it a little more objectively, and you look up your own name and then there follows a list of all the papers in all the journals of the world for that year in which a paper of yours has been referred to. I think that one thing that might be of interest to you that came out of my own perusal was that there were these one or two little schools in physics which were quite interested in what I'd been doing and I was completely unaware that they were interested in it. I mean they are working on my stuff and it hadn't got back to me, and this does suggest that communication isn't as free and easy as we often pretend it is in physics. Anyway, to get back to this question, when I think of my own creativeness, if you like ... I don't think I do see it as having periods of a few fat years followed by a few lean years — I don't really look at it like that. I suppose what one can do is go back and look at ones publications and plot them as a function' of time. As an objective criterion it would probably not be a very useful one; it would probably be very dangerous.

Meyers:

Yes, you could have had a backlog and been working out ideas you had thought up years back.

Wilkinson:

Yes that's true. Anyway, if dangerous as it is, you were to apply that system to my work, and you would find that there are no big gaps or anything.

Meyers:

I was asking for a subjective appraisal here, you know, whether it seems to you that — I'm thinking of years now not of short term — did your work come in spurts. You know, fertile periods...

Wilkinson:

From the point of view of ideas, yes. Well what I mean is that I've had probably four or five good ideas in my life, things that I think have changed the course of at least my bit of physics — some of them purely technical, some of them more academic, if you like, more fundamental. I mean I've done some things that have interested a lot of people and a lot of people have got on the bandwagon and started working on the same .thing. And that I don't think has gone in cycles. Of course if you've only got four or five in your life, so to speak, it is difficult to see them as cycles. So I think I probably would answer that it isn't conveniently broken down into creative periods or cycles, but there have been a number of creative times which have been rather generally distributed, say one every three or four years if you like.

Meyers:

I would like to jump ahead if I may to this Whitehead question which is relevant here. This is Whitehead making the statement that he had had no new ideas since the age of twenty-five and that everything he had done later has been elaborations of earlier insights.

Wilkinson:

Well, I think it depends greatly how you set your own standards, and that's why I find it a little bit difficult to talk. But in my own case whatever standard you adopt, I don't think that that is true. In this very irregular way, I've gone on having new ideas, and I've not noticed any change in my own ability to produce ideas. I feel myself as open to new ideas as I ever was, and I feel that I am as likely to have a good idea myself as I ever was. It probably depends quite a bit on the sort of subject that one is working in.

Meyers:

I usually think of a remark like that applying to mathematicians and theoretical physicists more than to most scientists. Biologists for instance who have to acquire a great deal of information firstÖ

Wilkinson:

Yes. I've noticed this in a lot of people, but in a slightly different way; they don't seem able to make the effort to assimilate a new idea. They don't feel that they can take a new idea and incorporate it into their own semi-intuitive ways of thinking. Perhaps the best example of this is the generation before and the generation after quantum theory came along. People now who are in their fifties, who would have already reached their middle twenties or late twenties when quantum theory came along, many of them do have a sort of great difficulty in handling quantum mechanical ideas freely and in an intuitive manner. They haven't got it incorporated into their common sense way of thought. Whereas the younger people, even though they may have no superior analytical abilities in manipulating the equations of quantum mechanics, are much better able to think in quantum mechanical terms. And this sort of flexibility of mind, what you can regard as common sense, is probably an important parallel study to this one on creativity. My own feeling' is that creativity is largely a matter of intuition and feeling. I mean these are sort of heuristic faculties if you like. I mean intuition is not quantitative, feeling is not quantitative, but it is what you use, at least it's what I use, in getting an idea. I suddenly, think well maybe nature is like this. And I feel quite strongly that to get that sort of idea, you do have to have some sort of, almost, feeling of personal contact with the problem. You know how things will behave and you know how the interactions will go. Well, in my sort of physics, which is sub-microscopic of course, one can never in principle have the classical kind of personal contact with the system that you're talking about, but you can get some sort of feeling for it. Many people work in terms of images and models and analogies and so on, and these work to some degree in that they enable you to make guesses and occasionally good guesses. But I think the chance of your making a good guess, of having a flash of insight or something, depends very much on whether you have this sympathy for the phenomena which lay the ground work for what you're talking about. And there I think it is the ability to incorporate something into your way of thought which probably gets a little difficult after the late twenties or the thirties.

Meyers:

You say that using analogies can be useful or misleading, is that right?

Wilkinson:

Well analogies, you never know how far you can trust them. The quantum theory of the atom in its primitive form, Niels Bohr's, of course is an analogy, if you like, with the solar system. You have a centre of force and you have things going around it. Well, that's all rot. I mean the electrons do not go around the nucleus in the sense that the planets go around the sun. Yet there is some sense in which they do; there aspects of the behavior of the atom which could be put into correspondence with the motion of planets around the sun. So if you start by saying to yourself, 'Could the atom be like the solar system?' you get part of the truth, and having got part of the truth, and having clarified the picture, so to speak, you can go on and develop it. And you get wave mechanics and the Schrodinger equation replacing the crude model of the circulating electron. But analogies only take you so far because they are only analogies. And the question is will they contain enough of the truth to encourage you to spend your time in going further, or for the world of science to spend its time going further. And that I think is what is important in the creative process. To have the faculty for applying analogies if you like. I mean, creation is thinking in new terms about a set of phenomena, and what guides you in your choice of new terms. I think that very very few people think completely in the abstract. I think most people argue or feel from a sort of system which they know and understand, into a new one. There's a very extraordinary illustration of that coming along just at the moment. There has always been of course, a dichotomy in nuclear physics between the study of the structure of the nucleus, which one thinks of as an assembly of particles moving in each other's fields of force in a very complicated way, and the properties of what used to be called the elementary particles, which were thought of as discrete entities each having its inalienable properties and acting as immutable building blocks for building up more complicated structures. Well over the last couple of years it has become quite clear that this is all nonsense, which the elementary particles do not exist in this sense at all. That one must think of the things which we used to call elementary particles as being made up of associations of particles, and one is now beginning to talk about what used to be called elementary particles in precisely the same way and in precisely the same language that we talk about nuclei. In fact the current issue of Physical Review Letters which I've just been looking at in the library here has an article in it called "The Shell Model of the Baryons." So now presumably one can begin to think about the elementary particles in the way in which one has thought about complex nuclei, which are complicated systems but with which one now has some familiarity. So just as one transferred ones familiarity with atoms, into nuclei, at a stage where one did not have the slightest idea what went on inside nuclei, one is now about to transfer ones familiarity with nuclei into the very constituents of the nucleus, the individual neutrons and protons. Of course, this is not going to be the right answer, obviously, but it's a step which will encourage us sufficiently to put a lot of effort in along these lines and maybe get a breakthrough analogous to the development of quantum mechanics out of classical mechanics. So I think in my subject one can see this happening very frequently. The big advances are usually made by analogies, transferring that with which one is already familiar to another system, a transfer which allows the new system to become open to your "common sense of ways of thought. Some people do, of course, advance in a different way, and I think Dirac is an example of that; some people will not say "Can I think of a semi-mechanical model which might reproduce the properties of the system?" They rather think, "Is there a mathematical structure which I could invent with which I might associate certain attributes of the system? Can I think of a group of transformations which are related to each other and under which the elementary particles will transform into each other?" This then enables us to collect together clusters of elementary particles which may have different properties but see them as essentially all the same particle broken apart into this cluster of different properties by interactions which are not invariant under the transformations that constitute the group. This is a very abstract way of thinking compared with the other approach. You don't in this approach attempt any dynamical picture of the structure of the particles, you ask a very general question, "What particles are closely related?" and "What group of transformations can be guessed"— it's purely a mathematical guess — "that will transform the particles into each other?" But the two approaches, the abstract approach of saying, "What is a complete self-consistent beautiful mathematical scheme? It and the mechanical model approach of saying, "How may these things actually be stuck together?Ē These are complementary approaches which converge and are not really opposed viewpoints.

Meyers:

These two techniques have kept pace with one another?

Wilkinson:

Yes, they have. One has only applied the group theoretical approach in the last twenty years or so, whereas the mechanical model approach, is the traditional British (Kelvin: "I want to see the wheels go round) kind of attitude to nature. This isn't to say that we haven't always had abstract thinkers in this country. Maxwell is a good example there — and everything that he said can be very succinctly put into modern language.

Meyers:

Your own inclination is towards theÖ

Wilkinson:

Well, I'm an experimenter you see, primarily. I get the answers but I'm also extremely interested, involved, in what the answers mean. And I think I said earlier that I don't like doing an experiment unless I know why I'm doing it in terms of answering some specific question, coming out of a theory or out of a model. My own understanding of the systems that I handle is much more in terms of the models than in terms of abstract systems. But Iím very interested in the abstract approach and I would like to see how that works out in detail. Do my exertions tend to be sustained or sporadic? I think I ought to say sustained there. I'm the sort of person who feels it a wrong if he isn't working. I mean I don't very easily lie fallow if I feel I ought to be doing something. And that has always kept me pretty well down to the grindstone. But within that or arising from that sort of pattern you see, there are periods when one rushes ahead and works all night for several days in succession. The rule is, looking back on it, that that kind of working has not been profitable. I advance very quickly but then afterwards there's a period of delay, and I think in retrospect I could have done just as well by taking it easier. My tendency then is sustained work, but I can't resist working unnecessarily hard when I get excited. This isn't because I'm afraid of somebody else getting in first. It's just that I'm desperately anxious to know the answer and I go on and on. Also I'm incurably optimistic. I always think I can do a thing more quickly than in fact I know I can do it. I donít know whether in your subject one has the same factors but in physics one says there is usually a factor of pi — if you've done it before it will take pi times as long to do it as you think; if you haven't done it before its pi squared. And though I find that this theorem is correct I'm always tempted when I'm a bit hot on something to work a little too hard. I don't learn by experience. Do I like discussing ideas with others? Yes, I find that extremely stimulating. Do I get new ideas as a result of the interchange or in the midst of it? Well perhaps I can take them the other way around. Almost all experimental work in nuclear physics is team-work — so I've had a long experience with team work. It's not uncommon these days for an elementary particle experiment to have fifteen or twenty names on the paper. But I don't like working in a team for the sake of working in a team. If it's advantageous for the progress of the work then I haven't the slightest hesitation in teaming up with somebody. But at the same time if I can do something myself, there is no technical point in bringing someone else in. So I'm very familiar with teamwork but at the same time I can also be a solitary worker. I think it's also true to say that the great majority of the papers that I've been involved with, have been my own ideas. I've started them off; I've not necessarily been the leader of the team because one does not usually work in an academic environment in that way, but in the majority of them I've supplied the starting idea, coordinated the work of the group. But then to go back to the early part of the question, I do find discussions very stimulating. I do often get new ideas as the result of interchange, in fact, I think most of my ideas for experiments as opposed to ideas for theories or quasi-theories, most of my ideas for experiments have come out of the interchange, by talking with somebody, by chewing it over and saying well, do we really know that such and such happens in this way. And then realizing, well we don't, maybe we should go off and measure it. But I've benefitted also in the more theoretical ideas, often not very directly. I do quite a lot of travelling around and talking and listening to other people talk, and I often say to myself, Look you ought not to do this; you're wasting time; you're not going to get anything out of going and lecturing to these people, you know them all already and you know they can't teach you anything so to speak. Oh why am I going off to this conference when I am only going to hear so and so talk and I know what heís got to say already? But in fact quite a lot of my ideas have come as it were unexpectedly, out of just such things as that, out of the struggle to express something clearly to people who, although they are your peers, are not quite in the field. Or out of the way somebody else is trying to express himself clearly to me, and maybe not succeeding. Out of this kind of thing I've frequently found my own ideas coming along. I've realized there is a gap in our understanding of a particular process, or something of that sort, because I had to try to get it across in presenting my talk or I've seen somebody else struggling and waving his hands where he obviously isn't able to think particularly clearly. Then there is another phenomenon of going to a conference and not really being interested in what is being talked about, and having a rather vacant mind, and just being superficially occupied in what the chap is talking about on the blackboard, like on a holiday you're superficially occupied with not falling off the path or something of that sort, then under those circumstances also I've had the sort of uncorrelated ideas that∑ come along that have been valuable. In this case it is not an interchange of ideas; it's sort of an interchange of intellectual environment. Somebody is talking about something that I am not particularly interested in, and for some reason that I don't understand at all, either because of what he's saying or because it's occupying a part of my mind that normally vetoes my original thoughts, I don't know, but whatever the reason, under those circumstances, I often get a thought. But also I've got ideas out of things which are further removed from the actual subject matter of the discussion, and I wonder if this isn't connected with another phenomenon I noticed in myself (I call it the bath phenomenon and holiday phenomenon) that if I go off on a proper holiday, then for a few days, maybe three or so, I can completely abandon myself to the holiday, walking or whatever it is, with the kids or going around seeing sights, and I can keep work completely out of my head. But usually I find that after a few days, a problem will come into my head, a work problem, and usually it will be a problem that I didn't know that I was interested in, or that I used to be interested in a long time ago. It's not, under those circumstances, as a rule anything to do with the last thing that I was interested in. And sometimes it surprises me in that I find myself thinking something that I didn't know I was at all concerned about. Several times, I've had quite a good idea, which I subsequently followed up, that has more or less actually dropped on me out of the blue. This thing that I described as my most recent good idea that I've been developing during the summer; that came to me I think it was in May. I was invited over to Halifax, Nova Scotia for a meeting of the Canadian Association of Physicists. I didnít particularly want to go but I thought maybe I ought to and so I went and listened to a number of talks that I wasn't particularly Interested in. And one of these talks was on an aspect of elementary particle physics that I. had not been particularly interested in before, and the speaker was explaining that, on very general grounds, one might expect a certain type of relationship between the masses of elementary particles. And it suddenly struck me that well, these same arguments as far as I can see, would apply to nuclei, you would expect the same relationships to hold for nuclei. Why has it never been checked? It's a general relationship. Almost in the same thought I realized why it had not been checked, that certain critical information just had not been available in the nuclear case and I wondered how one could get this information. I didn't see how to do it. But another talk that I went to at the same meeting provided me with the answer. I mean the man wasn't in fact talking about this, but in his talk he gave me a clue to the way in which one might get this other information. So I went away and thought about it and it turned out that one could analyze very new data that are just becoming available during these last few weeks in this way to supply the missing ingredient, so that's the kind of luck that I've had several times, but I think it's a luck that comes to those, what is it "Dans les champs de l'observation Ie hazard ne favorise que les esprits preparís" (Pasteur's famous quote). I think that's right. It's been something that I've always believed, that luck goes and settles down in those places that are prepared to recognize it. I think that if I have a talent it is for this kind of open-mindedness, or an ability to take in ideas from one field and to apply them to my own. Have I had ha ha experiences? Yes, I have that; I frequently had the flash of light kind of thing, but again this links up with the previous question in that, on sufficiently large numbers of occasions to make me quite sure it's significant, I've had these experiences not when Iíve been thinking for myself but when I've been trying to explain something to somebody else. This procedure is so valuable that I sometimes do it deliberately: if I have a half-baked idea, I try and transmit it to somebody else, even in its half-baked form, because in formulating it over and over again I am quite likely to hit upon something which would clarify it and carry it further. "Have you ever had the same experience when the experience was a false one?" Well, I'd say yes, I have had the ah ha experience and it's turned out to have been wrong. Not very often — when I have these things they usually turn out to be right — but I have also had it wrong. This may link up with another property of mine, like this pi and pi squared one that I can't learn from, and that is that I always think I know where north is. Put me down anywhere under any circumstances and say "Where is north?" and I always feel I carried it out, but in fact I'm as often wrong as right. Why I have this feeling heaven only knows.

Meyers:

You are not using a metaphor. You're talking about geographical directions?

Wilkinson:

Yes, I feel I really know where north is. Again by experience I know that I am likely to be 180 degrees out as in the right direction. I've always had this, one might think that it was because of my interest in bird navigation; the ability to find north is a very important element of bird navigation. So I know I'm capable of getting this feeling of rightness and sureness and being -wrong about it. So I have to watch out for that. Are there any particular types of mistakes that you are prone to make? Well, this judgment of how long things take is a mistake, but perhaps not in the sense that you mean here; if I could rephrase it another way and say, "When I have gone wrong in my physics what sort of errors have I usually made?" I think they have come — I may say first of all that I have never made any absolute howling bloomers, but I've made a few mistakes, and they have chiefly been of the character of over-estimating the accuracy of the measurement, in particular over-estimating the limits that I can put on the degree to which something is not there. Often in nuclear physics it is important to establish that a certain transition or a certain radiation or something is not present, and obviously the confidence that you can put. On your statement that it is not present is all important. One says that a particular branch of a radiative transition is weaker than one percent, let's say, in terms of all the radiative transitions that take place. And I have found myself prone to be over-optimistic in the limits that I've set. Well, this is something that I've learned never the years, and I am now much more conservative than I used to be, but you can put this another way and say that I've been too trusting in the analytical interpretation of the instrumental responses or that I put too much literal faith in the resolving power of a detector.

Meyers:

You found yourself doing that when it came out in the direction predicted; did you find yourself doing the same thing when it came out in the opposite direction?

Wilkinson:

In what sense, in an opposite direction?

Meyers:

You're using here the inaccuracy of the equipment on your own side, but do you use the inaccuracy of the equipment against the equipment if things don't come out as predicted.

Wilkinson:

I'm not really blaming the equipment here, I'm blaming myself. You see all apparatus produces a certain response, a reading as a function of time or distance or something of that sort. And in order to interpret that response you have to have a theory of instruments of some sort. I've always been interested in theories of instruments, in fact in the early days I spent a lot of time working on the theory of the Geiger counter, and the related instruments, and what I'm saying is that I think that I have on a number of occasions, placed too much reliance on the theory of the instrument and not insisted enough on an actual experimental verification that the instrument, at that particular time, was working in accordance with the theory. I think that, on a somewhat deeper level, the sorts of mistake I tend to make areÖI think that would be overÖ critical of myself if I say that I tend to take sides with theory. I mean I do have certain theories or models that appeal to me more than others, and let us say that I'm happier when an experiment agrees with a theory that I'm fond of, than when it doesn't. Now that's not in the slightest to say that I in any way suppress the results that conflict with a theory. Obviously I wouldn't, but I think my researches probably have been guided a little too much in the direction where I thought that the results were going to confirm a theory. This is a tendency that I fight against very strongly, and in recent years I have deliberately made myself do experiments in directions where I felt that the results may not be going to agree with the theory. Because my own experience in physics is that you make progress more rapidly by disagreeing with something than by agreeing with it, that nothing is put forward unless there is a certain body of evidence in its favor, and I think you make more rapid progress by finding exceptions and understanding the exceptions than by piling up further examples in confirmation. So this is a sort of strategic mistake if you like, that I've tended to amass more evidence than is necessary, flogging a dead horse or whatever you would like to call it. I think I may have had too much of a tendency to "overkill" a problem that way.

Meyers:

There's a question related to this about whether you have ever doubted an empirical check which failed to support an expectation because the expectation seemed too good to be wrong?

Wilkinson:

Well, yes, in the sense that I think that most experimental physicists are prone to this sort of logical error; I'm more likely to repeat a measurement if it doesn't agree with theory than I am if it does. And I realize that there are great dangers here; if you have a lot of points which ought to fit on a line, and if you just re-measure those that don't, you're likely to regiment the line; you ought to re-measure at least a few of those which do fit the line to see if they don't move off it. But I think that's just the shortage of life expectancy, which makes one want to re-measure first the things which appear to disagree badly. Of course there are clues here. If a certain body of data does fit a theory very well, and a few points don't, then this is an invitation from nature to go and look at those few points and make sure that they don't. And that is what I would do, and what I do. Certainly not to say, "Well these measurements are obviously wrong; we won't include them in the final data." I mean that's a rankly dishonest way of going about things. I have on one or two occasions published data in which one point did disagree with the others, and for some reason or other had not been able to repeat it. But "(would never because the conditions of measurement were poor assume that that was why the point was off the line and so not include it in the results. I've had enough experience to know that you just have to do that. Quite often there is really some significant feature there which takes a few points off the line. And then you're cutting your own throat very badly to ignore a piece of information because it doesn't conform to the rest. But at the same time this isn't quite answering your question because my first reaction, if I've got a nice theory which I like and some of the data conform to it and some of them don't, my first reaction is well, I'll re-measure these points. If they stay off the line then that's exciting. Then there's something you really don't understand and you have to spend time on it. The reason may turn out to be trivial — the apparatus isn't working properly. Physics — all science — is full of instrumental effects which have been misinterpreted as being genuine physical phenomena. My own tendency, since I am interested in instruments, is to spend quite a lot of time over such aberrations, and more often than not I have found that they are instrumental. Have you ever had scientific ideas stimulated by fields outside of science? Well my other interests in life, even if you leave out family and so forth, are outside of science, particularly music, graphic arts, architecture, and bird watching if you care to include that. So I have plenty of contact with other fields. But as for specific ideas, I don't think that I can point to any. There is one thing here which I don't think was talked about which is extremely important at the deep level and that is the way in which one makes scientific judgments. There's very little question about applying the well-defined laws of physics like conservation of energy, angular momentum and momentum, but of course one rapidly gets into the field where you are either questioning the possible existence of new laws of physics or youíre making rather radical new theories, originally out of the old laws of physics applied to the new situation, or and this is a very exciting thing, finding circumstances which appear to demand the invention of new laws of physics. And for what it's worth, my own definition of a law of physics is something which is sufficiently absurd. If you get a result in physics, which you completely fail to accommodate within the present structure of the laws of physics, in other words, if the difference between the result of the experiment and the theory based on the existing laws is sufficiently big then you say, I haven't the slightest chance of understanding this. There must be a law of physics which says that this is so." In fact this is how the laws of physics are discovered. One writes down a new law if you aren't capable of understanding what you're seeing within the framework of the other laws. And so it is often a question, "Should I invent a new law of physics to explain these data or shall I make some ad hoc patching up of the old laws, supplement them in some way?" or "If we have alternative hypotheses within the existing laws of physics how do I choose between them?" And when we come to these questions of choice, either of sticking with the Old, laws or supplementing them, or alternative hypotheses within the old framework, how do we make the choice? My feeling is that this is essentially an aesthetic type of judgment. One uses very much the same criteria in deciding between hypotheses as one uses in deciding what is a good or satisfying work of art. Well, there may then be a feedback here if one is interested and involved with conventional aesthetic matters like music, graphic arts and so on, one may in effect be training aesthetic powers of judgment that can then be profitably applied — if unconsciously — in choosing between theories or choosing between hypotheses and so on. I have quite often backed the right horse, when other alternatives presented themselves, just on the basis of my feelings which are the only court of appeal that one has when things are otherwise equally acceptable. And it may well be that Iíve been helped in my lucky guesses by having a strong interest in purely aesthetic, matters. One often does try to separate out the scientific method and scientific ways of thought from the humanist methods and ways of thought, but I think that in the end the two are probably very closely connected, at least this is my own interpretation of the way in which I myself have very frequently found' myself thinking.

Meyers:

Could you elaborate a little about these aesthetic feelings in the context of a specific idea or hypothesis.

Wilkinson:

Well, I think that's very difficult because itís like saying, "How do you feel good when you look at a picture? It is a feeling; it is not a rational process at all. One feels that whatever it is one is considering is satisfactory, that one gets something out of it. It may be disturbing or challenging as some painting is; it isn't a comfortable feeling, always, but there's a feeling either of rightness about this, which I suppose is a comfortable feeling, or a feeling of promise, challenge if you like, as a lot of so-called modern art is; you feel you have to struggle with it and put a lot into it yourself. If it is going to speak to you have to interact with it. And to me some modern art is good because it gives me the feeling of a worthwhile attempt to understand it, to make progress with it, and some is bad because it doesn't give me that feeling. And I get just the same sort of feeling when I see alternative ways of describing a set of data, alternative theories. I may not understand either of them; they may both be rather repulsive in a certain sense but I will usually have the feeling that one of them is worth carrying through and struggling with and the other one is for the birds. I reject it. And I then have sort of an emotional block against committing myself to the unappealing theory, and I may be wrong. Just as I may be wrong on the modern art.

Meyers:

You can't be wrong about a work of art in the same way because there is not that checking stage.

Wilkinson:

No, but there I'm perfectly prepared to accept the judgment of the community. Of course, you'll have to wait a long time — 100 years or so sometimes. I've done a little bit of a study of this, particularly in music, looking back, say, a couple of hundred years, what music was available then and what music has lasted. I'm particularly interested in the pre-baroque periods, up to and including Bach if you like but chiefly before him, and I've done quite a bit of going back and playing a lot of music from that time; I do find that I like best the music that is supposed to be best, not all the time, not uniformly, there are a few composers whom I think are real good who are not big names, but by and large I comfort myself that the judgment of posterity is more or less right. Right, of course, for our time, because oneís appreciation of a work of art surely depends on one's epoch. And some work which was very popular and commanded wide support in certain eras I find revolting. Pre-Raphaelite art, for example, I cannot stomach, and it had an enormous vogue. I think I can understand why it did; but I can understand such art only intellectually, I can't understand it emotionally. So I do grant the absence of a quantitative criterion in art but I think there is Ďright' art and 'wrong' art, although, of course, one can't press that too far.

Meyers:

Would you go as far as Dirac in your aesthetic approach to theories?

Wilkinson:

You mean when he says that it is more important to have beauty in your equations than that they should fit the facts? No I donít think so. Not quite. I mean I'd like to, but I'm a practical person and I have to live more or less from day to day and that means that I have to be quite highly empirical. Dirac, I think, would also claim to be an empiricist to a certain degree, but heís an empiricist in that he makes an empirical search for beauty. He's not an empiricist in the sense that he takes the data as they are and fits an empirical equation to them. He has a whole spectrum of equations and makes his empirical choice from among them, the ones that give him the best feeling. I don't know how far to go in this argument: "We make the world rather than study it." That the human being is only capable of certain forms of awareness, is only capable therefore of certain ways of thought, certain ways of providing associations between his sense data, and so obviously must understand the actual world within the limits of his own intrinsic capacity. And one can conceive of, though of course, can't in any way describe, another sort of being with different modes of awareness of the natural world that would describe a different sort of world. I suppose itís rather like Plato's shadows on the wall of the cave; we're not really studying reality in a complete sense; we're studying projections of reality, onto planes represented by the way in which we are constituted as human beings. One can conceive of different sorts of projections and the world as we know it is just one aspect of a much more complicated world. I don't quite know where that takes one. I suppose what I'm saying is that one should keep a very open mind about the natural world, and always be on the lookout for phenomena which may give us clues about other aspects of it. It may be that we have sensitivity of a very poorly developed kind to signals of a type different from those we normally respond to; maybe there are other methods of linking us with the world than those we normally study, but linking us very deeply. I'm not a spiritualist or anything but I'm thinking of some kind of possible connection either involving time or possibly space which can link different points in time, maybe; I don't know. I mean one has to go into science fiction you see. But we do have a number of mysterious phenomena in the world that we don't understand at all, and maybe they are clues, whispers, of a way in which a more complicated understanding may come about. And, of course, if such a thing were found it would wholly and radically change our ideas about the world and about ourselves. And so while I think one mustn't go around the bend on this, I think scientists (and the harder headed the scientist the more it's true) have to keep a very open mind. And of course if such a thing were established it would be the biggest step forward ever made. But it is not the kind of thing which one can go out and hunt for I should think. I've got a kind of feeling that there are closer connections between the outside fields and science, but I can't think of any at the moment. (Pause) There are some fairly trivial connections, which I think it's really unfair to say come from outside fields. You know that different musical instruments have different timbre, depending on the mixture of harmonics and things of that sort, well, this is a kind of emotional feeling which is of use in nuclear physics in that nuclei, in a certain sense, can be put into states by vibration, analogous to the vibration of a column of air in a clarinet or something, and I have myself on occasion made progress with an idea of that sort more rapidly because I was familiar with music. But that I think is really cheating and not answering your question because it is familiarity with what is really the same physical phenomenon in a different experiment; it's not nearly as interesting as saying 'Are there any musical experiences as such which have been valuable?' But on the level of experience the sort of feeling that I get with the various arts are very similar to the feelings I get when I meet a nice theory. That's not to say that it's direct help except possibly in recognizing when something is right.

Meyers:

Well, we'll have to leave that and go on to information — processing machines, whether this development has had any effect on your thinking.

Wilkinson:

Hm, well, that I don't understand. I don't think there's any effect on thinking. There's a big effect on doing, is this what you mean? That one may have a number of problems and one may tackle any of them. In the past one had criteria to determine which problem you would tackle; now, an additional factor in deciding which to tackle is whether you can put it on a computer or whether a computer will help. Is that the sort of thing?

Meyers:

I had heard the phrase 'man-machine complexes' and I was wondering whether it had gotten to the point where scientists were thinking of the machines as extensions of themselves.

Wilkinson:

Oh yes, very much. I personally have not been very much involved in this, but one of the big pushes we're making in this laboratory now is to construct a pattern recognition machine, that will essentially replace the human eye in perceiving regularities so that one will be able to scan bubble chamber pictures at a very high rate rather than employ the army of young girls we do at the moment. And, of course, you have to train the machine how to recognize the thing; you have to put it in possession of the same faculties that you use if you do it yourself. So in that sense it is a very direct extension of one's own ability. I'm not directly involved in this but it's something I spend a lot of time thinking about. I haven't used it yet in my own work but I hope to later on. I'm completely sold on the idea. Although, one can be seduced by computers and start regarding them as the object of the exercise rather than the physics. But it hasn't yet reached the stage where the availability of the computers does affect the ideas that you have. It may well be that the ideas that you have are affected by your potential ability to put them into practice. And the capacity of the computer may enter in a more-or-less unconscious way. How do you go about selecting problems for following up? I don't really know. At any one time I probably have in my head half a dozen problems I would be quite happy to work on. I think this is related to a question you asked earlier: I tend to be a sustained sort of worker; I don't sit around thinking what to do. I think I've found that certain of my most interesting experimental work has been done accidentally. I've embarked on some problem and then discovered some side turning which was more interesting than the problem itself. This has happened over and over again. (I remember at school, if I was faced with, say, five essay questions on an exam, I would just start writing and then find which one I was — answering later. And I found something analogous in my nuclear physics.) Do you keep a notebook of ideas or did you ever? No I never have. A very few times in my life I thought I ought to and jotted down a few notes, but I've always lost them and have no idea where they are. But I don't usually make them. I keep them in my head, and if one drops out of my head I reckon it's because it's not that interesting a problem. How do you keep up with the literature? That's a terrible question. I don't know whether it's a good idea to keep up with the literature or not. The abstracts of work in progress are terribly useful to tell you who is working on what.

Meyers:

What is your general strategy in your approach to the literature, considering there's so much of it?

Wilkinson:

I'm afraid I don't have a very coherent one. I read through the titles of all the articles in several journals regularly. And then there are a few other journals which I just look through casually, mainly because they come to me one way or another. But I think I've found empirically that I get along better ignoring the bulk of the literature than I would if I went through it thoroughly; it would take too much time to go through it all systematically and I think too, that I would get discouraged reading too often about people who are working along the same lines or parallel to myself. This has not affected my work adversely but I think that one reason for this is that I've always been an opportunist and jumped on a problem that has come into topical importance and as far as possible I've tended to make new types of problems. And if one is trying to do novel things, the chance that there is an overlap in the literature is very much less. But this other thing, "How widely do you read outside your area of primary concern?" Oddly enough I find that I sometimes enjoy reading carefully an article on an aspect of physics which is remote from my own. I usually do this at night, perhaps when lím probably in a slightly dopey state but I have found that it's paid off occasionally by having relevance to my own work. Also I take one or two ornithological journals, but this is entirely separate. The next question about how much is creativity the result of discipline and how much the result of unconscious inspiration, I don't knowÖ I suppose the right answer is that one is no use without the other. In my own work I think the will and discipline part has been essential in providing the field from which the talent and unconscious inspiration have arisen. As I explained, ideas tend to come to me in a rather random kind of way; but I don't think that I would make any progress by sitting in the sun and waiting for inspiration to come along. Talent alone is not enough. If somebody is able to do something he should do it and not lounge around sitting on his potential so to speak. At what stage in this development do you like to show new ideas to colleagues? The stage at which I show new ideas to colleagues depends, I think, on the type of idea. Some ideas can't be shown to be wrong unless one does a lot of experimental work and there I do the work first before talking about them, but if theyíre of a more specimen kind where there could be some flaw of a technical character, then I usually talk about them with somebody I believe could detect such a flaw as soon as possible. But I don't spend all my time dashing down the corridors talking with people; I don't like that sort of colleague. I like an idea to be at least half baked, before it is exchanged, I don't like it in its completely liquid state. So I don't feel it necessary to be talking the whole time. To state it quantitatively, if I was working full-time I would probably go out and seek a colleague for some reason or other, not necessarily for a new idea, but possibly just help, probably on the average of twice a day. What is your response to criticism? I don't mind at all. I have no feeling of awkwardness about someone thinking that my idea is a silly one, I'm quite happy to be criticized along those lines. And I'm also quite happy to have my ignorance pointed out. I think this is another way in which one's work can be held up, if you don't discuss it with people because you're afraid of being shown up. And I personally have had to face that problem a great deal because though I'm an experimenter I am very interested in theory and have done a fair amount of work of either a completely theoretical character or half-and-half character. And I recognize that I am no technician as a theorist and there are many places where I could go badly wrong simply by ignorance of the actual technical details of what I'm thinking about. But I am not inhibited by that. If I can get to the point where I can recognize that I don't know (that in itself is a very important ability) I go and ask someone whom I know knows. So I have been quite dependent in quite a bit of my own work on encouragement of that sort from people who are in the theoreticians' union rather than the experimenters union. Before the age of twenty? I think I always thought that I would end up as a physicist, probably from the earliest time. My physics teacher was a very vague person who never taught me anything but who gave me the impression that there was something very exciting; my chemistry teacher was a very dry and precise slave driver who taught me how to work like hell but didn't inspire me with what he was actually teaching. So there was that sort of interplay. And then when I got to Cambridge for the first two years I did chemistry and physics equally, but that confirmed that it was physics that I wanted to do. What sort of physics was determined partly by chance in that I was drafted into the atomic weapons business during the war, but I would have chosen nuclear physics in any case; it was already a fairly firm incipient interest. Relaxation? I very much enjoy relaxation, although I'm not very good at doing nothing. I like to, in away, but I find myself a little nervy about ritually lying in the sun or something of that sort. I used to be quite active in the theatre and for several years was the theatre critic of the Cambridge Review, the Cambridge senior members' weekly journal, and then I suddenly realized that I wasn't enjoying this, that I had to go to the theatre every Monday night and have my review into the printer by Tuesday morning. This was unenjoyable and furthermore I hadn't enjoyed it for quite a long time. So I stopped doing that; and my wife used to do it with me, and we said well, we won it go to the theatre any more until we really want to. So from going to the theatre regularly once a week we didn't go to the theatre for several years, except casually. And then quite recently we started going again. Church architecture is my big outside activity. For example this last week I had to go to Cambridge to give a talk to the undergraduate physical society and the next day I was distributing prizes at a school in north Lincolnshire and then came back here, and when I do a trip of this kind I plan it entirely around churches. I have a number of studies of church architecture and I do my homework and plan a route before I go. So that's a form of relaxation that I enjoy very greatly. I don't read a very great deal, not as much as I'd like, maybe one novel a year or a couple. I read plays a little though not very much. My reading is chiefly reading about art, and I read a little poetry, not much biography, a little bit of travel. And I spend as much time as I can with kids; I enjoy family games, whichever game the kids might wish to propose. But more than anything I relax with music. I have a good collection of records, chiefly relatively early music. And I do a little myself, though very very poorly.

Meyers:

In your reading, do you read much in the history or philosophy of science?

Wilkinson:

No I don't. I think I probably have a wrong attitude to the philosophy of science. I've not very much use for it, although some aspects of it I find very interesting. I'm quite interested in epistemology but I'm not interested in the philosophy of the physical method, not particularly interested in what philosophers say about scientists' ways of thought. I think I probably should be because quite a lot of my own ideas are philosophical or semi-philosophical — the business we were talking about earlier today about the relationship between science and aesthetics for example. I don't have much interest in the history of science. I've not been very interested in the history of ideas — whether this is a sort of arrogance I just don't know. Iíve just not had time for it so far. I should say that those of my colleagues who remain practicing physicists but are very interested in the philosophy of science are not the best of my colleagues. What part of your work do you enjoy most and is enjoy the right word? I don't at all mind using the word 'enjoy' in connection with my real work, which is doing physics, I do enjoy it enormously. I'm constantly astonished that anyone will pay me for it, I enjoy it so much. The work that I do here at Oxford, which is purely administrative, trying to get money and build up a department, I hate it all and I'm not paid half enough for doing that, I hate it even though I have an intense emotional involvement in it. If the place collapsed now I'd be done for. All my interest and activity in my everyday life is concentrated on getting a proper laboratory set-up going well, But the actual mechanism of doing it is what I dislike so intensely. There are some aspects of physics which I don't enjoy. I mean I don't enjoy the rat race aspect of it, although I don't find myself very strongly affected by the rat race. When it makes one's colleagues behave in an unpleasant way, which is what I don't like. But cutting that out I think that I enjoy the rest of it. Have you ever wished that you had gone into another field? I think from time to time I have, but not for intellectual reasons. I don't feel that another field is richer intellectually than my own, but I have occasionally wished that I was in a field where I could work when I wanted to, which of course I could in nuclear physics if I were a theoretician rather than an experimentalist. I've never considered renaming myself a theoretician, despite the fact that I do theoretical work, partly because I do enjoy the experimental procedures of physical science and partly because I haven't got the technical equipment to be a theoretician. I could acquire the tools, but that would mean in effect going back to school for a couple of years and that I can't contemplate. So I think I'm making an uninteresting answer to your question. Yes I have wished I had gone into another field but not for intellectual reasons. Doubts about the value of my work? Well, I frequently recognize that what I'm doing is not the most exciting thing in the field, but I've never had any doubt that I was making a useful contribution. And from time to time I have thought that I was making an exciting seminal contribution. So I've not been worried about that question in any deep sort of way. "Personal life?" Well, I think that I've been extremely lucky in my marriage in that I married someone who has never made the slightest objection to my working as concentratedly as I wished. I have had periods when I worked extremely hard and everything has been pushed on one side for it, and there have been no family difficulties when those times came around. "Particular emotional state?" Well, I don't work well if I have emotional worries. At the moment let us say I have worries about running the laboratory, and even when I'm away from it my mind is constantly filled with problems related to it — ''Will we be able to get enough money to get the new computer?" — and so on. These things are always in my mind. I think that I am at my best when I have a relatively tranquil state of mind, a mind undisturbed by worries about external matters. In fact my work is not interfered with by worries about by worries about how it's going to come out. But I can't compartmentalize my life and have a certain amount of time when I worry about this and a certain amount of time when I worry about that. "Physical surroundings?" I like views but if the view is too nice I tend to find myself admiring it or indulging in some sort of Walter Mitty type expedition consequent on looking out over the landscape instead of working. I think most of my work has been done in places where there was an uninteresting view. The only time I had a view was when I had an office in the Clarendon Laboratory. It was high up and overlooked the big open area we call The Parks where all the cricket is played. And I did tend to find myself standing up and peering over The Parks and pretending to be thinking when in fact I wasn't which is very nice but doesnít get any work done. I'm rather tolerant of circumstances for many things. I can go to sleep very readily almost anywhere, for example, I've even fallen asleep in an awkward situation like a ski lift, and got carried around the top. No my work is not a compartmentalized part of my life, I carry it always with me and I'm as likely to worry about work at home or anywhere else as I am in the lab, with the exception, as I say, that if I do take a deliberate break in my work then I usually leave it behind satisfactorily for a few days. The holiday seems to saturate me in a very little time. On a smaller scale the same thing happens if I go to a concert or to a play or to a gallery. For the first half hour or so my work is left behind, but it usually gets in before the evening is half over. Again in a gallery I satiate quickly. I can concentrate on pictures for an hour or so and then the freshness is lost. Is there a relationship between solving problems in work and in life generally? I think my tendency is to say yes to that. I see myself in life thinking and acting similarly as I do in work. For example, in ordinary life and also in work I find it awfully difficult to regard something as having achieved the final solution. Most things that I have done in my life have been somewhat open-ended in that they have suggested other problems. I try and finish off a given piece of work as completely as I can, but it's only rarely that it doesn't apply to something else and I think I tend to find that true in life as well. I find it rather difficult to stop doing things completely for example. Coffee tobacco, alcohol? I don't need incentives at all. I can work absolutely in a vacuum when I'm working at physics. I quite often have a bit of a drink in the evening, usually at a time when I'm doing some long stale administrative work. I'm not a smoker, I don't suck sweets but I'm extremely fond of a little alcohol. I certainly drink every day. I normally make myself a martini or drink a glass of sherry before supper. Coffee I don't need. I drink coffee at coffee times; I drink tea at tea time, but that I don't need although I enjoy it. I don't know about constructively channeled sadism at all (pause). I don't know. I enjoy twisting knobs if that's of any help.

Meyers:

Have you ever been interested in Freudian psychology?

Wilkinson:

No I haven't. I find it amusing, in fact hilarious, what I've met of it and I've not the slightest intention of denying its relevance or truth. I suppose this is true of almost anybody but I don't consider myself in need of psychiatric adjustment. I have very good friends who do go in for it, in fact I have a couple of friends in Greenwich Village who spend g 800 a month on their psychiatrist, and they enormously enjoy being told by him just what rotten creatures they are and proving it to each other. And as I say I find it hilarious but I'm not interested. I've never read any psychology systematically or did anything of that kind but I certainly don't dismiss it. "Reputation, support of colleagues, and security vs. the disinterested search for truth" I'm not at all sure about the disinterested search for truth. I do nuclear physics because I like doing it. The other things, reputation — well it's nice to have a reputation, it's nice to get invited to conferences and things of that sort, but I don't think it's critically important. I mean I enjoyed physics in just the same way long before I got invited to conferences and things of that sort. "Support of colleagues," what does that mean?

Meyers:

I was thinking of something akin to reputation, but in regard to the colleagues who are closer to you.

Wilkinson:

Esteem, something of that sort. I like to think I have their esteem but I don't know whether I've got it or not. It's very difficult to know whether you have it with colleagues in this country. In the States I know that I have it from a number of people that I respect and I value it. But it's not important to me in the sense that I have to know. Security, I've never had to worry about because I've had tenure for as long as I can remember so material security never entered into it. Have you ever been depressed rather than stimulated by the achievements of others? Yes I suppose so. I've occasionally felt, "Oh hell, how can I compete?" particularly in recent years when I've been able to give only a small fraction of my time to work. I've been made envious rather than depressed, I suppose, by people who not only 'can do it every day but don't even have the distractions of teaching, as well. Like at the National Laboratories and so on. But if you're talking about it in the rather deeper sense about being depressed by the quality of the work of others in the field I think no, although I do recognize that in many of the things that I am interested in there are many people with considerably greater talents than mine, and I enjoy seeing them exercise them. On at least one important occasion, Iíve withdrawn from a field because I saw coming into it people whom I knew were very much better equipped for carrying it further forward. But this I didn't mind because it was a field that I had opened up myself. This is one of the things I spoke of earlier, an essentially theoretical business, where I supplied the seminal idea and when I pushed it sufficiently far forward to excite the theoreticians proper, they rushed in, and I withdrew; I was very happy about that situation.

Meyers:

What about early heroes?

Wilkinson:

I think I explained that I didn't have any teachers but that I was self- taught in nuclear physics. I didn't have any heroes at that time. I'm not a hero maker; I don't really look on scientists as heroic figures. I do in art, in music and certainly in architecture. Those are my heroes, not scientists. I think possibly because scientists I usually know too much about. You usually don't know much about a painter's bad and unsuccessful paintings, while most scientists have shown feet of' clay in some aspect of their work at least, either wrong or trivial. And this gets in the way of elevating them to a hero figure. I think I do have slight heroes now. Wigner, I would count as a hero; I suppose I ought to say Rutherford although somehow I don't really feel that. But he was a great man and Iíve always respected his achievements. In a sense they were too obvious, but this is the problem that someone who opens up a field suffers from a little bit: the work appears crude to later generations.