INTERVIEW

Steven Chu

Interviewed by Anne Jacobson

This article also appears as a Profile in BioMedNet's Conference Reporter.

Posted March 16, 2001 · Issue 98

Background

Biography
Steven Chu is the Theodore and Frances Geballe professor of physics and applied physics at Stanford University. His research was the first to show how to cool and then trap atoms with light, and the first to show how to trap and study single molecules with optical tweezers, a technique now widely used in biology to study DNA, RNA, and proteins. The 1997 Nobel Prize winner in physics, he splits his research time among the diverse fields of atomic physics, quantum electronics, polymer physics and biophysics. Here he explains why, for researchers, "it's a good time to be alive."

What event led you into research?

When I was growing up, I was always interested in science. I come from a family that had a strong emphasis on science; all of my brothers and cousins were interested in science. It was the ambiance, and it was a typical Chinese upbringing. In second grade my father would tell me what to do and what not to do. "Don't get married until you get a Ph.D.," he'd say, which was unusual advice for a second grader.

Who has most inspired and/or influenced your work?

I had a terrific high school physics teacher. While I was an undergraduate at the University of Rochester there were a number of professors who took me under their wing, so I got a lot of attention. My Ph.D. thesis advisor also had a tremendous influence on my career. He encouraged me to tackle big things, not just little things. I stayed there [at the University of California at Berkeley] as a postdoc, also working for him.

Then I went to Bell Laboratories, and it was like an awakening. In those days, Bell Laboratories was one of the meccas of science. They had just come off a hiring freeze, so a couple dozen of us were hired within one or two years. We had a lot of intellectual freedom as far as what to pursue, so in that way it was not a standard industrial lab. Imagine tremendously smart senior scientists, as well as go-getter junior types; it was like you've just been allowed to enter Mount Olympus. The halls were alive and buzzing. Anything that happened in the areas of science that were covered by Bell Laboratories - kinetic matter physics, quantum electronics, materials science, and some astrophysics and biophysics. We didn't have to teach, and we didn't have to worry about funding. All we had to do was science. It was like an extended postdoc.

Bell Labs really opened my eyes to a much wider range of science than I would have seen if I had stayed at Berkeley. I was made assistant professor at Berkeley but took a leave of absence to go to Bell Labs my first year. So had I stayed I wouldn't have had as quite a broad influence.

The group of people who entered Bell Labs at the time I did are now all big shots in science. Four of us have Nobel Prizes. It was an extraordinary caliber of people.

Who awarded you your first grant and what was it for?

My first grants were from the National Science Foundation and the Air Force. They both funded me essentially immediately after I left Bell Labs to go to Stanford. It was for laser cooling and trapping of atoms.

What was your best experiment?

First let me define "best" as something that opened up a field, where people took what happened and used it in their own work. My best experiment, then, would be the demonstration that you can use light to cool atoms down to a few millionths of a degree above absolute zero, so-called optical molasses. That work led to many of the things now called laser cooling and trapping, which was probably my most important work of the stuff I got the Nobel Prize for.

There are other experiments that got a lot of notoriety when they happened, but they were bringing closure to an area of science or achieving a very difficult piece of work. They were tour de force experiments, but didn't lead to opening up a new area.

In about 1990, I started using optical tweezers to manipulate and observe single molecules. This was some of the beginning work on single molecules, which has become very fashionable in the last few years. I was doing single molecule experiments on macromolecules, such as long pieces of DNA and polymer physics.

In the mid-1990s, there was a discovery, quite by accident, in an experiment on how polymers unraveled. We found that they would take different paths, a completely unexpected result. The idea was that if you have identical molecules and identical conditions, the polymers would follow very different paths was not in the consciousness of the polymer community. What was really nice about this is that we could go back and look at all of the other experiments that gave conflicting results, and now we could understand why there were conflicting results. It wasn't that the experiments were wrong, the underlying assumption was wrong.

It really opened our eyes to the idea that single molecule experiments were not just a neat little parlor trick, but that they could be used to discover some new things. At that time, in the early to mid-1990s, virtually all we knew about chemistry and biology was from experiments done on systems of many, many molecules. The atomic physicists had begun to do experiments looking at individual atoms or ions, and from my background as an atomic physicist it was just a natural extension to what we were geared to be thinking about. So my group started working in earnest, using single molecule methods to ask biological questions. It has become very fashionable, but using single molecule methods is more than just a fashion. There are things you simply cannot learn otherwise.

In a talk I heard just today, someone asked, "Do you really need single molecules to do this?" The right answer is that sometimes you don't. But sometimes single molecule experiments are easier. In my lab, we do bulk and single molecule experiments. The bulk experiments are harder because the signals aren't as clear and there is much more interpretation that has to be done. With these newer techniques you can just look at molecules. You don't have to have a preconceived notion of what to expect. The design of the experiment doesn't necessarily have to be hypothesis-driven.

What was your most disastrous moment in the lab?

It was related to my most important experiment. We had done an experiment to cool and confine atoms, and we made a mismeasurement. We published a paper, and the preliminary results of our measurements was that atoms were being cooled to 180 millionths of a degree above absolute zero. Theory had predicted the coldest temperature this particular atom could be cooled to was 240 microKelvin, a little bit hotter than our 180. But as scientists, we wave your hands and say, "you can calculate this." It wasn't a big discrepancy, but a little clue that there might be a problem.

In the next year or two there were other little clues that there was a problem with our laser cooling experiments. Things started to go wrong; they were working better than expected. In science, this is very unusual. We call this a strong violation of Murphy's law. Finally a colleague said, Why don't we go back and measure the temperature, but much more carefully. So they remeasured and found that if you get rid of the magnetic fields, even the earth's field, you can get the temps down not to 240 but 40 microKelvin, a temperature much colder than we thought was theoretically possible. It was big news.

All these little clues that there was a problem, followed by this clue. We thought, What is going on? There was a mad dash to figure out how our theory went wrong. Another group figured it out, and I figured it out and reported the results a few months later at a meeting. We figured it out within a few weeks of each other.

So why was that dissatisfying? Well, we had the first little clue. If I were really paying attention I would have taken this little clue, dug into it and figured out what was going on. It wasn't a disaster, but I missed it.

Which scientific idea (yours or others') do you regret the most?

I can't think of any. That's the great thing about science. There are checks and balances. If you do something that gets other people's attention, then they are going to want to repeat it. . . . So if someone messes up, others will catch it.

Science is really a collective effort. In science, in the end, it better be making sense to everybody. For that reason, the foundation of what is being built will not go away. There are certainly experiments that could go wrong, but after a while the field gets it right. Science marches on like that.

What is the greatest unanswered scientific question?

There are an amazing number of questions. We don't know the structure and the scale of the universe. Science has progressed enough that we can start thinking of these questions, where 50 years ago you simply would not think of them. The whole science of cosmology - questions like "Where did the universe come from?" and "Where is it going?" - is now an experimental science that's been lifted from philosophy.

There are some nagging feelings of uncertainty about our microscopic world, namely quantum mechanics. It is intuitively very unsettling. The only good thing about quantum mechanics is that it seems to be right. You can predict things that enable you to make a transistor laser, which you would not have been able to make without quantum mechanics. Yet it remains very unsettling.

From very basic questions in physics, you can ask questions about more complex systems. How does the brain work? How do we store memories and how do we think? Is it really true that we are just a bag of chemicals and synapses and gates and ion channels? Is what we see in our consciousness just a collection of simple things added to a certain size and complexity, then all of the sudden you get an amazing result?

So there is no single frontier; it's layered.

I truly believe that science is driven by new methods and new tools. We can sequence DNA, we can invent a patch clamp, we have X-ray crystallography and NMR to determine structures, and so on. It's with these new tools where we see big surges of activity and progress.

What are your current research interests?

My research interests right now are a combination of my older field - atomic physics and laser cooling and trapping with cold atoms, and the newer (to me) fields of biophysics and polymer physics.

Since we understand atoms and their interaction with light so well, I sort of regard this field more as engineering. . . . For example, we developed methods for making so-called fountains for clocks, and within a decade our method became the time standard for the world. We also used cold atoms to make cold atom interferometers, where the wave-like nature of the atom allows us to separate the atom up to a centimeter apart, and bring it back together again. The interferometers make exquisitely accurate and precise measuring tools. Some of the best inertial sensors are made using this technique, and fundamental constants can be measured better by this technique than by any other. So we are going to work hard on that field.

There is another part of me that is using single molecule methods to continue doing work in polymer physics. There are a number of outstanding questions that have been around for decades that have been answered by this technique, and there are many more that you can answer. We are patiently going down the list and picking questions we think are important.

Then finally in the biophysics realm: I'm torn, because this is a much bigger field for polymer physics. We are doing a number of things. We are trying to understand the folding of proteins and RNAs. These new single molecule techniques are good for complementing the other things we now about proteins. Really, they offer a unique window to these folding problems. We are studying a number of RNA molecules, in part because we are hoping to find some general physical principles.

Receptor binding, signal transduction through cell membranes, vesicle fusion: all of these ideas are ripe for single molecule work. Of course it's ridiculous, because I don't know any biology. But I don't want to leave any of it, because it is really new and it is feeling very much like the early days of laser cooling and trapping. Then, no matter what we touched, things were working. There were whole new sub-fields we opened up. And this single molecule work feels exactly that way. It's a good time to be alive.

What are the qualities of a successful researcher?

You have to pay attention to the real details. Out of the 50 things you have to do right for an experiment, you only have to get one wrong and the experiment fails. But you also have to know how to step back and say, is this the right path? Is this the right problem I should be thinking about?

You can settle into studying your enzyme, your molecular reaction, or your part of the whole landscape. But it may be that what you know and what you have would be better used on something else. And that's tough; it requires that you make a big leap. But good researchers are able to make those leaps; especially good are the people who become experts in one field, then bring their bag of tricks to another field.

You also have to be tenacious. You have to be able to pick yourself up off the floor when things aren't working. You have to keep at it, with one caveat: you have to be able to step back and know when it's not going to work.

It helps to be smart, I suppose, but maybe not as necessary as one thinks. It helps to be lucky. As I tell my students, if you have to choose between smart and lucky, choose lucky.

At the time I was at Berkeley I was lucky; there were about six or seven Nobel laureates there. So I watched them and how they worked. One of the things I found was that they were very attuned to knowing what was the new technique, the new technology. They asked, "Is new technology about to break, and if so, can I nudge it along to make it break?" Those practices are things I've used in my entire career.

How do you feel about winning the Nobel Prize?

It has affected my life more than I thought it would. Now I'm asked to do a lot of interviews and give "old man" talks. There are more public service things I feel obligated to do, because as a Nobel laureate I am considered a spokesperson for science.

When I look back 20 years ago when I was a postdoc at Bell Labs, I see that life was simple then. I could go in the lab and do my thing. Even when I was a department head at Bell Labs I was spending 80 percent of my time in the lab, with my own hands, running experiments. And that was a lot of fun. Now I have a moderately large group, so I'm partly an administrator, which is a drain. But I am helping to train students and postdocs, so then it becomes worth it. Many of my students are going out and starting very successful careers. They are now better than I am.

Anne Jacobson is a freelance science/medical writer based in Atlanta. When she finishes her master's in public health in May, she hopes to move to a city with more snow.