Interview: Peter Feibelman
1996 Medard W Welch Award Recipient
Interviewed by Janice Reutt-Robey, October 16, 1996
REUTT-ROBEY: Hello, my name is Janice Reutt-Robey. I'm a Professor of Chemistry at the University of Maryland. Today I'm speaking with Peter Feibelman, who is a distinguished member of the technical staff in the Surface and Interface Science Department at Sandia National Laboratories. The occasion of our meeting is that Peter is the 1996 recipient of the Medard Welch Award. This award is one of the highest awards given by the American Vacuum Society. It's conferred annually in recognition of seminal contributions in fields of interests. They are specifically research contributions in fields of interest to the American Vacuum Society. Peter received this award for his insightful predictions and explanations of surface phenomena based upon first principle's calculations.
Peter, following your Ph.D. researching many-body phenomena, you've essentially spent most of your research career working on surface-related problems. What drew you into surface physics?
FEIBELMAN: Well, actually, when I started working as a many-body theorist in San Diego, in fact my nuclear physics thesis had to do with the surface of the nucleus. My thesis advisor directed me toward experiments that had been done which showed that, when a neutron penetrates the liquid drop, of which a nucleus is composed, that there was evidence that surface waves were excited, and my job as a thesis student was to account for the experimental data and explain what surface waves were being excited. And then at the conclusion of my Ph.D., I went off to Paris - I went to Saclay - and I didn't really want to continue in nuclear physics particularly. And at that time, a sabbatical visitor from your own institution was there, namely Professor Arnold Glick. And when Arnie heard my talk about my thesis, he pointed out to me that a normal mode had been thought of and discovered at the surfaces of metals, called the surface plasmon, and suggested that maybe, if I substituted long-range forces for short-range forces, I could go from the nucleus to solid-state physics, and so I did that. I actually worked out a theory of surface plasmons, and I published it in 1968. And then when I was looking around for a way of getting back to the United States and applied to Urbana [University of Illinois], Charlie Duke had noticed it, and I think he was very interested in having me come because of that work, and perhaps in ways I didn't even realize, guided me into becoming a surface scientist without my really anticipating it.
REUTT-ROBEY: It's convenient that you mention Charlie Duke's name because you and Charlie, and actually one other theorist, are the only three theorists - at least whom I know about - who have won this Welch Award in the more than 25 years that this Award has been given. One thing one might wonder is, do you try to make your theoretical studies accessible to experimentalists?
FEIBELMAN: Well, I have always enjoyed communicating with experimentalists. When I was young, I knew that I was reasonably gifted mathematically, but I never could figure out how mathematicians knew the difference between an important problem and a problem that was not interesting. Whereas in physics, nature and experimentalists made it quite clear what was important and what was less so. And when I arrived at Sandia Labs, where I've spent most of my career, it was also made clear to me, as well as to other theoretical people who were there, that our job was to communicate with experimentalists. Fortunately for me, I've always enjoyed doing that, and so, in carrying out my job, I did what I found very pleasurable anyway.
REUTT-ROBEY: In the work that you've done in your career, how important has collaboration been? And if you wouldn't mind, perhaps you could describe a few of the important collaborations you might have had.
FEIBELMAN: Well, in the beginning, it was not so important. In the beginning of my efforts in surface science, I was working on the theory of electromagnetic fields at surfaces; it was a kind of follow-on to my thesis project. And actually, as time went by, it got frustrating because I was making quite interesting discoveries, but nobody seemed to want to find out whether they were right or wrong. And it actually took a while before I managed to be invited - well, I didn't manage, I was invited -- to a panel discussion where I met Ward Plummer, whom I had met before but hadn't had a chance to have such lengthy and serious discussions with. And I told him about the discoveries that I had made, and I wondered whether there weren't some experiments that he could do to show whether they were right or wrong. As it turned out, I kind of launched him on a new career direction, and we've had a very fruitful collaboration since that time. I mean, already in Urbana, I learned to collaborate with Duke, and I enjoyed that quite a lot, but the collaboration with experiments was something quite new and wonderful to me.
Perhaps I should take a step back and say that when I was at Stonybrook [State University of New York], the opportunities for collaboration were fairly limited. There was Franco Jona's group, and I decided that if I was going to survive as a theorist, I had to get in contact with an experimental group that would provide me with inspiration and information. And so I actually think this was a very important step in my career, I decided I would start visiting IBM and offer my services free, for nothing. And so I made contact with Dean Eastman, who farmed me out to Warren Grobman, and I got to meet a lot of people there and ultimately wrote two papers with Dean, which were among the most read papers I've ever written, and were very helpful in getting me a job later on when I needed one.
At Sandia, I've had marvelous collaborations. Almost immediately on arriving there, I started taking an interest in Jack Houston's Auger line shape measurements and found that I could explain features of them that were hard to explain any other way and which the experimental group there had not thought about. And in getting serious about Auger, without realizing it, I was preparing myself for the day in Jack's laboratory -- I should say, in Jack's lab at three in the afternoon, we had Coke flip, so everybody in the surface group would get together and flip coins to see who would go down to the vending machine and buy Coca-Cola or ice cream or whatever for the rest of the group. And it was at one of these Coke flip events that Mike Knotek showed up with a bunch of data that he just could not fathom. In particular, he had been irradiating titanium dioxide surfaces and observed oxygen plus [O+] ions coming off, but only at a rather high threshold - a threshold which he actually proved coincided with the energy to ionize the highest core level in titanium, and he was wondering what ionization of a core level had to do with causing oxygen to desorb. And my Auger experience had prepared me to give the answer on the spot, and we had a very exciting six months after that, which led to a serious new understanding about how a particular process of radiation damage works, which now bears our names, which is kind of nice.
Later on Wayne Goodman arrived on the scene, and he had done beautiful experiments relating catalytic poisoning and promotion properties in real-world catalysts to similar properties which he could study on single-crystal catalysts, and that got me very excited. And so there was again an opportunity for me to bring my theoretical wisdom, prowess, whatever, calculations at any rate, to bear on that, and I would say that that was again a fruitful example.
And perhaps most recently, having written a large computer program, I decided to study phenomena associated with surface diffusion and came up with a novel mechanism for diffusion to occur of an aluminum atom on an aluminum surface. And after talking about this several times, one day I was giving a talk at the March meeting and Gary Kellogg and Tien Tsong, both of whom had heard me talk about this before, were just sitting there, and something clicked, and both of them went home and realized that they had data in their desk drawers that verified that this mechanism occurs. I don't know if you call this collaboration, but the fact is the constant ferment of ideas and interaction just leads to good things happening. At Sandia, we just have a very interactive group. I mean, you hear about in other places where there is very much a sort of internal competition and not much communication. It's never been that way at Sandia; it's always been great, and I attribute my own success as a theorist very much to that atmosphere. And I should say that at Maryland, you have a similar atmosphere, and I think it must be wonderful for you there as a consequence. I would hope that more universities would develop that kind of collegial atmosphere.
REUTT-ROBEY: So in describing your collaborations, you've also essentially described a little bit in some of them, major problems that you've worked on. I think it's really remarkable that, in your field, you've really made some important contributions in very different areas, from surface electromagnetism to stimulated desorption to diffusion, chemical structure and bonding issues. One of the things that I would like to know is, as you've progressed from one problem to another, was there a clear point where you knew it was time to move on to the next problem?
FEIBELMAN: Certainly, and that's why I did. In a way, it's a little sad, but the surface electromagnetic field project was marching on. I was doing what I thought was quite well, but nobody was paying any attention in the form of experimentalists. And so at a certain point, I decided, "Peter, you have done enough." Also, I thought at that time that I had done most of what was easy, and I think, over the years, I got a sense of how much time and effort I should risk on a project compared to the reward that was in the offing.
And in particular, in the electromagnetic fields area, I had done a lot of work on jellium - nearly free-electron metals - and I had struggled with the more complicated materials where the crystal field was really essential, and I finally came to the conclusion that if nobody was going to help me on this, it would be nuts for me to go on. And in the meantime, surface science as a field started to shift. In the early '80s, one started to have the sense that the surface structure problem, which had been the focus of everything in surface science in the earlier years, that surface structure problem pretty much seemed to be solved. People had more powerful computers, they had more data, and they had the sense that there were now systems where we really knew where the atoms are and so we could start to try and understand, for example, chemical effects on surfaces. But we could start to understand processes because we had a database that was sound. And so, whereas my earlier work had to do a lot with interpreting experimental techniques, I now wanted to get into predicting phenomena. And of course at the same time, the local density approximation had been improved to the point that you had the sense a) that it was predictive, and b) that you could do things in a finite amount of time.
I don't know, I wouldn't say that I planned very much my shifts, but I've always been, how shall we say, opportunistic in what I hope is the best sense of the word. In about 1978, Joel Appelbaum and Don Hamann approached me at a meeting and said-- I mean, I knew them pretty much from being in surface science. They said, "We've written a new computer program that we think will really enable us to predict properties of a whole variety of surface materials. Unfortunately, our computer power at Bell Labs is not extraordinary, and we wonder whether you would like to get involved with this because we know that, at Sandia, you have big computers and lots of time." And I thought, "My goodness, for a guy who was trained in nuclear physics and for whom everything previously had been jellium (so no crystal field), this was a great opportunity to learn about "real solids.'" So I jumped on that.
And then of course, when Knotek and I were at Coke flip and we had this flash of insight, I dropped everything for several months to exploit our success. But I think the basic theme has been to exploit what I know, to take advantage of opportunities that come my way, and to kind of keep a nose to the air and have a sense of what's important. And so switching has been something that I wanted to do for those reasons.
I would like to say, for whoever pays attention to this tape down the track, there are some people who seem to have a gift for what they call "skimming the cream" and who tend to flip from one problem to another like a butterfly from one flower to the next. That's never been my way, and I think that it takes a rare genius to succeed at that for very long. And so it's always been important to me to have a long-term project to which I feel a sense of commitment. It doesn't necessarily involve my entire career but that will involve my publishing a goodly number of papers and lead me to some insights that make a difference.
REUTT-ROBEY: Well, you've referred to "Coke flip" at Sandia National Lab as one important event there. And in fact, much of your career has been at Sandia National Laboratories, although I believe you've had brief sabbatical stints at IBM and KFA Jülich. To what extent has your location at Sandia National Laboratories influenced your selection of problems and essentially the scope of your scientific efforts?
FEIBELMAN: Well, Sandia Labs obviously has had a mission, and the mission has changed somewhat over the years as politics and the world have changed. I had from my management the sense for a long time that it might be a better idea for me to work on semiconductors than metals, which for a variety of technical reasons and history, I had been working on. It's kind of amusing that with the takeover of Sandia by Martin Marietta, now Lockheed Martin, I work for a metals company, not a semiconductor company. And so the pressure is off from that perspective.
I think perhaps one thing that's been very wonderful at Sandia for me is that the ratio of theorists to experimentalists has been just right, in the sense that there's always been some experimentalist there (because we are heavily experimental) who is doing something that I feel I can bring my efforts to bear on. And so I've never lacked for somebody to talk to. And it's also a place, as I mentioned earlier, that's very collegial, so I've not had the sense that I have to compete with my colleagues or get out front.
Also, I think an important aspect of life at Sandia - perhaps this isn't so different from other labs; I haven't worked at other labs - is that our management, from the top to the bottom, until quite recently anyway, has been all scientists. And so these are people who have a real understanding of the importance of research and the way researchers' minds work, and they've been wise enough to cut us the slack we need to do the things we do. It's not often easy to explain to our paymasters why we're doing things the way we are on a sort of a short time scale, but having scientists who are in charge who themselves have a record of performance and contribution to the national research enterprise and so forth, that's made it a lot easier. So we feel that we have their respect, and the country feels that they are trustworthy in what they say. And all of that has led to a stable environment.
I guess maybe I'd also like to comment about stability of funding. One thing that has been terrific at Sandia - again, of course we're susceptible to the real world, as is everybody - but for the longest time, we were simply a line item in the national budget, and that means that we could embark on long-term projects and not have to respond to a product cycle very rapidly, or a quarterly report. And the increasing emphasis on short-term funding and perhaps the degree to which accountability nowadays is overdone, absorbs a great deal of our time and makes life somewhat less pleasant than it used to be. Still, things are pretty terrific at Sandia, and very few people ever leave, except in a box. [Chuckles]
REUTT-ROBEY: Well, since this tape will be watched, presumably, by younger viewers, I was wondering if you could comment on what you find the most difficult aspect of your work now and perhaps comment on whether that's changed over the years.
FEIBELMAN: The most difficult aspect of my work, the thing that I find hardest, is the incessant attention to detail that's necessary. I think that in some ways, in our schools perhaps, we select people the wrong way to go into science. And I don't know, here I am winning a prize, so I probably shouldn't say I was selected for the wrong reasons. Nevertheless, a scientist is somebody who tries to make order out of chaos, and you have to accept dealing with a chaotic situation and have faith that despite your lack of understanding of what's set before you, that you'll get there.
In training people for a career in physics, we sort of give them the impression that physics amounts to solving the problems at the end of the chapter, but life just isn't like that. We hardly know what the problem is oftentimes, and formulating problems turns out to be very hard. Then, I don't know for a theorist - I mean, sort of life with a computer program or figuring out which approximation is likely to be right or wrong or knowing which experimental data to trust or not to trust -- just requires so many questions and so much attention to detail, and you really have to have a taste for that. It's also, I wouldn't say it's been hard for me; I have a lot of perseverance (it's just built into my head), but perseverance is certainly a major aspect of succeeding at science. If you want immediate reinforcement, don't go into science. I can tell you that.
REUTT-ROBEY: Well, probably many people in the audience are familiar with your very successful 1993 book, A Ph.D. Is Not Enough, which offered very stimulating and entertaining advice to people who had recently received their Ph.D.s and were embarking on scientific careers. If you could make some changes in the way Ph.D.s are educated, what changes would you make?
FEIBELMAN: I've been thinking about this quite a lot, and to me, the most important aspect that seems to be missing when we get young people coming through Sandia, for example, is a seriousness, an intellectual seriousness about science. The thing that I want to see from somebody coming in is the idea that this is not just fun with high-tech toys and that every little experiment that we do is sui generic (there you go, Latin!), that something that's important in and of itself and has no relation to where we're going. Science is the development of a story about how nature works, and I want people to take very seriously the aspect of developing an understanding of nature as the focus of their work. I want people to come and have a sense of the intellectual history of the field that they're working in because, only if they know where we've been, can they do something useful about where we're going. So I would like to have, perhaps, professors ask students to, in their last year, write a sample grant proposal with all the elements in it. I think that it would be a great benefit to the students to go back through the literature, dig out what's important, get a sense of who the names are - what they did, why they did it, and why the problems that are being worked on now are important. I think that that will enable them to write better resumes, be more successful in their interview trips, and hit the ground running.
I also think that, in an era when there is a big focus on alternative careers - we hear a lot of sadness about how you can't go on in a traditional career - I think it would be very interesting to educate students about alternative paths to the career that they want. For example, I know several young scientists - and I think perhaps this idea applies mostly to experimentalists, more so than to theorists - but I know several young experimentalists who, after their undergraduate work, or at least before completing their Ph.D.s, went off to an industrial laboratory and worked as technicians in a laboratory where professionals were doing science. And in this way, they got a serious sense of who was a good scientist and who was a bad scientist. They got a sense of what problems are significant and what problems may be less significant. And then when they went back to graduate school, they were just able to roar through their doctorates in a way that people following the normal track could not. And when they came out to give their job seminars, they were much more sophisticated, much more mature, and have done wonderfully well. I don't see much of that in the education system now.
I should add, and this is something I say in my job lectures, it's not bad being a technician for a couple of years before you go to graduate school, because you earn some money. And having money in the bank makes your life much nicer as a graduate student. You can pay a babysitter, you can live in decent housing, and you can spend a lot more time thinking if you don't have to worry about where the next bag of groceries is coming from!
REUTT-ROBEY: Surface science today and in the 1970s when you began your work - what are the big differences?
FEIBELMAN: Well, in the 1970s, it was not clear that we would ever do anything realistic. And as I was saying earlier on, the surface structure problem was the big issue. We did not have a handle on how much impurity of whatever kind is on the surface, and we had even less idea of where anything is sitting on the surface. And those were obviously the keys to moving forward. But the biggest problem was enormous divergence between the promises we were making in our grant proposals and what we were actually working on. I mean, we said we were going to revolutionize catalysis; you know, we talked about lubrication and adhesion and a host of practical applications at the end of the rainbow. But in fact, we were seeking to work on problems that were as simple as possible. So every atom was equivalent to every other atom, every surface was as symmetric as possible, and we were really working on fundamentals. And we were doing this for perfectly good reasons - namely, you can't run before you walk. And nowadays, we live in a world that is very different than surface science. Actually, the surface structure problem was pretty much under control before the advent of the scanning tunneling microscope. For example, the famous 7 x7 structure was actually solved by TEM [Transmission Electron Microscope] people in Japan before the STM came along. Nevertheless, the STM has been an incredibly wonderful addition to the repertoire and other high-resolution microscopies, and we are now flooded with data about realistic systems. And to me, it's just terrific, at the age of 54, to see the possibility of something real happening before I retire. So I think that's great.
I think the one thing that's really missing now is…or how shall I say? One thing that I would like to see changed is: I would be happy to see a few more theorists getting out into surface science. At the conference that we both recently attended, it was amazing to me to see how many experimentalists are spending their time doing simulations, perhaps not at the highest level, instead of doing the experiments they're capable of, which would be at the highest level. I think that theorists should be doing more of the theory and experimentalists should be more in the laboratory. And I would like to see research management people devote more investment to bringing theorists into laboratories and fostering a situation such as I have had, which has been wonderful, at Sandia where one or two or three theorists can work with several experimentalists and everybody's work is the better for it.
REUTT-ROBEY: I think I'll close this interview with probably the most difficult question, which is "where do you see the biggest research opportunities in surface science today?"
FEIBELMAN: Yes. Well, I've been thinking about that one.
REUTT-ROBEY: We can turn the camera off. [Laughter.]
FEIBELMAN: I just want to hark back to the last remarks that I made. We are now living in a world in surface science when the science has become more mature, and making promises and fulfilling promises are not so divergent. Surface science has been well-funded for 30 or 40 years now, but because the promises that we have been making all along have been so exciting. I mean, devising materials that will be useful for making a host of technically wonderful things, from X-ray mirrors to better catalysts to materials that are structurally stronger and so forth, are perhaps now more at hand. And I think, with the immense improvement in our ability to look at realistic systems, we have a shot at doing for people what we've been telling them that we would do all along, and I hope to contribute to that. I'd love to see visible consequences of my insightful explanations before I leave the field, and so that's my response to that.
REUTT-ROBEY: That's the end of my questions, so I'd like to thank Peter for meeting with me today in this interview and discussion of his insights on the field of surface science. Thank you.
FEIBELMAN: Thanks very much, Janice, and it's been a pleasure being here. I hope somebody benefits from this down the track. Thanks a lot.