Steven Chu Interview: Conversations with History; Institute of International Studies, UC Berkeley

A Scientist's Random Walk: Conversation with Steven Chu, Nobel Laureate, Physics; Geballe Professor of Physics and Applied Physics, Stanford University; February 13, 2004, by Harry Kreisler
Photo by Jane Scherr

Page 4 of 6

Nobel Research in Physics

Before we talk about this new link that you're working on between physics and biology, let's talk a little about your research that led to the Nobel Prize. Give us a sense of how you came upon that problem set and what you, in fact, did. It's related to atoms, lasers, cooling, and so on.

[It began when] I was at Bell Laboratories. There are two main branches of Bell Laboratories. The main research branch was in Murray Hill, New Jersey. In 1983, a director [at the other branch] in Holmdel asked if I would become a department head in his division in Holmdel. The director, by the way, is Charles Shank, who's [now] the director of LBL. He said, "Well, Steve, why don't you consider coming down and starting a new department which would be a basic science department here?" Holmdel had excellent laser science and laser engineering, and a lot of the great things that have come out of optical communication were spawned at Bell Labs in Holmdel and Murray Hill. I said, "That sounds like a great job." So I went down and started this department, and started hiring people, and also inherited some very talented people. Actually, two of them are here, also: Daniel Chemla for a brief moment was in my department, now a division leader at LBL; and Jeff Bokor, who's a professor in Electrical Engineering, was also in this department.

There was another really wonderful scientist there named Arthur Ashkin, an older department head. I started talking to him casually, in the hallways. He had this dream: "Wouldn't it be nice if you can hold on to an atom with light?" He had tried to pursue this dream in the early seventies, in the mid seventies, but it wasn't really working. They did some very key experiments demonstrating the fundamental forces, but it wasn't looking like they were getting closer to really holding on to atoms with light. Finally the management told Ashkin, "It doesn't look like it's going to work; you've got to move on to other things." But then I came on board, and I was this new, young person who he could corrupt.

"You go do this."

I started thinking, "Okay, this sounds pretty interesting," and I started having a look at it. I started doing a lot of calculations. It was getting to be bad, and I was thinking, "I can see why you quit." I didn't tell him that, but I was thinking to myself, "It's not looking good."

There's a few "eureka" moments you're going to have in science. Mostly they're gradual eurekas, which I can come back to later. But there was this time.

It was not looking good at all; I would try it this way, that way. It's all on paper -- not looking good. And finally, there was a big snowstorm in New Jersey. They said over the P.A. system the forecast looked very bad. There's going to be nine inches or something; the lab is going to be closed, you should all go home. Now, I live very, very close to the lab, so I said, "Oh, heck." Everybody left, and it was very quiet. It was one of those beautiful things where you can see the snow falling down and everything's turning fluffy white, and maybe it was appropriate [to think about cooling an atom] because it was snowing.

I found you can do an end-run. The [conventional wisdom] was first, you hold onto an atom; then you get it cold; and then you can do what you want with it. I said, "Well, what if you reversed it? What if you cooled down the atom first? Don't hold onto it, but maybe in the process of cooling it down, it's going to hang around for enough time that you can have a chance of grabbing onto it." And so [after] a little calculation I said, "Holy smokes. This looks like it's going to work."

And then I said, "Well, I want to refine the calculations." So then there's the gradual "eureka." I wanted to refine the calculation. So you're surrounding this atom with light, and it looks like it's getting very cold, to the point where your feeble little trap that was going to hold the atom could work. But it needed to hang around for a while. So I started to say, "Okay, tomorrow I'll come in and I'll start to write a program to predict how long it will hang around." I start to write the program. Luckily, I'm not that good at writing programs -- I'm good until about three lines -- because if I was really good at writing programs, I wouldn't have thought about it at all and just written the program. So I get to three lines of code and said, "I've seen this problem before. Einstein solved it."

Good old Albert.

What he did is, he looked at a dust particle in the fluid; he was studying Brownian motion. Here's this dust particle being battered from all sides by atoms and molecules. He said, "If I take this particle and I move it, there's a viscous drag in the fluid, and that slows it down. The reason it's being battered around is because of random imbalances between pressure from the left and pressure from the right." What I wanted to calculate was how this particle would wander around, because the previous day, I'd shown it had this viscous drag on it. and that you do have these fluctuations. I was going to write a computer program to say, "Okay, step to the right, step to the left, and balance all the forces," but I thought, "No, I can use this solution. I know where it is. It's in an elementary textbook, an undergraduate textbook. It's the 'random walk' in a Brownian motion medium. You just plug in those numbers, and voila, you get ... wow, it's hanging around for a long time, because it's a random walk!"

And so I got very excited. I went to my boss, Chuck Shank, and said, "Look, Chuck, I know you're not keen on this, after years of research, but this is so simple it has a shot at working. You can get it cold, you can hold onto it, and we can go from there." He thought about that and he said, "Well, okay, you've earned the right to do something crazy, but don't try to recruit someone else." So I said, "Okay, okay, just my post-doc and my technician. " Because if you're onto something really big, you want to bring in your friends and say, "We want to go fast; we want to do this and ... "

So we puttered along for a few months, going like the blazes. I talked to Art about it, and he went, "Hmm, hmm, okay. It's not the way I dreamed it. Okay, that sounds promising." After a few months, it began to look like it was going to work, really going to work. And I said, "Come on, join in, and it's going to be a lot of fun." As I indicated in my lecture, it worked much better than anybody expected.

What are the implications of what you discovered in a layman's way of understanding?

Once you get an atom very cold ... and cold is really the average speed that an atom moves. The atoms in this room are moving at speeds of supersonic jet planes. In fact, that's why the speed of sound is what it is. It's just determined by the speed of molecules. Once you get an atom really cold, so it's moving as fast as an ant walks, a fraction of an inch per second, then very, very weak forces can push them around, and you can do what you want with them -- for example, using electric or magnetic fields, or light. You can hold them, you can push them around, you can do things that you simply cannot do when they're whizzing around like supersonic jet airplanes.

The ability to hold onto and control and manipulate these atoms means, for example, you can toss them up; they can turn around due to gravity in a vacuum can where there are no other atoms around, and you can make better atom clocks. You can make what are called, atom interferometers. You quantum-mechanically split the atom apart, so one part of the atom is the quantum wave going to one region in space; the other part is the quantum wave going to another region of space. That atom interferometer can be used to measure acceleration or gravity or rotations with very high accuracy -- in fact, in terms of acceleration or gravity, better than any other way of doing it. And in terms of rotations, certainly better than any commercial or even laboratory grade laser gyroscope.

So all of a sudden, you can measure changes in gravity so accurately that it's going to become competitive with the current ways of measuring changes in gravity, which is useful in all exploration. You can probably put it on an airplane or a helicopter. And with global positioning satellites to tell you the height and changes in distance, and inertial sensing systems, and something that measures change of gravity over distances on a scaled meter, it opens up the opportunity to do map gravity drains and pockets of oil, diamonds, things of that nature, minerals, on a very fast-moving platform like a slow-moving plane or helicopter. So there are real practical implications. Already the world is on the atomic clock standard, defined by so-called atomic fallons of atoms.

The atom interferometer was totally unexpected. It just popped out. People, even the researchers in the field, [find it] hard to think about what you can do with it, even if you force yourself, until you have it in hand, and you can then begin to see the abilities of this new method or technique. It's only after we had it ... and then not only me, my group, but the world in general. No one was talking about any of the applications that came out until we actually had it and we saw how powerful it was, and then began to appreciate it. You can force yourself to think of what might come about, and you can write down a few things, but you're going to get only a small fraction of them. That's the wonderful thing about science.

And actually, it harkens back for me to what you had said about your high school experience, in a funny way, that learning to look at something and think logically about it, and "Wow!" you're taking it to a new level. Not that you were doing Nobel Laureate a work in high school, but some of the elements are there in this work.

Yes, I think that is true. But it's also just letting something happen. This is one of the things I did learn at Berkeley, and I watched great scientists here. Many of them were doing something that, in hindsight, looked very natural. They would say, "Here's an emerging technology. With this emerging technology, can I ride piggy-back on it? Can I use this technology to turn it backwards and do some new science?" Normally, you would think, "Oh, basic new science discovery; turns into a technology; you make a better widget." But what I appreciated when I was a graduate student here was that that's all true, but you can also take that technology, turn it around, and you can use it. A good example is radar. During World War II, the U.S. and Great Britain, especially, developed microwave engineering methods to have microwaves transmitters that allowed radar, so that we can measure and see things far away. The scientist who helped develop that radar, and other scientists who could see the power of that technology, seized on that shortly after World War II. A string of Nobel Prizes came out of people who used this new technology to do great science. Charlie Townes here [at Berkeley] is a prime example of that. His knowledge of microwave science -- during the war he was working on microwaves.

At Bell Labs, too

At Bell Labs, that's right. After the war, he said, "I want to do microwave spectroscopy, because here's a new tool." We now control of short-wave multi radiation. And he became one of the leaders in microwave spectroscopy; wrote a classic book with his brother-in-law, Arthur Schawlow, and then invented an idea of stimulating the emission of microwaves called the maser. The extrapolation of those ideas from microwaves to optical wavelengths led to the laser.

That's one example of using technology -- first, building on technology during the war, saying this is a wonderful way, a new scientific tool; use it to do science. Then wanting to improve the tool to get to show the wavelengths, and voila, you had the laser. I saw this over and over again. When Charlie came to Berkeley, he wanted to use his knowledge in lasers and microwaves to do astronomy. So, again, he was going to ride the technology. And I was looking around and saying, "Yes!"

Now, he's a brilliant scientist, but the lesson I learned was you don't even have to be brilliant if you're the first to look at something with a new tool. So I said, "Okay, what are the new tools?" When I was graduate student there was something called a tunable dye laser. I told my advisor, "This is a wonderful thing. It's only a few years old. This is a tool that we should be using, now let's go figure out some science to do with it." Luckily, there turned out to be some very fundamental physics questions you can address using this tool.

It's the fundamental physics that drove [Townes]. From my side, yes, I was drawn to the fundamental physics, but also "Let's use a new thing to do it." If you use an old tool to tackle a problem, you've really got to be smarter than the rest of the folks, because everybody has this tool. If you're the first to look at something new, it's like discovering your world. You just look around and everything you see is going to be new.

Next page: Bringing Physics to Biology

© Copyright 2004, Regents of the University of California

See also the Charles Townes interview, Adventures of a Scientist (February 2000)