Charles Townes Interview: Conversations with History; Institute of International Studies, UC Berkeley

Adventures of a Scientist: Conversation with Charles W. Townes, Nobel Laureate, 2/15/00 by Harry Kreisler.
Photo by Jane Scherr

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The Habits of a Scientist

Help us understand more about doing science, because many young people might not have the fortunate background in this rural setting that you have. In your book and in your description now you're conveying to us a sense of the discovery. Help us understand what it takes to be a scientist. One thing that you talk about again and again in your book is that often you turned failure into opportunity, for example, not getting the first teaching position as you went into the job market, but rather going into an industrial lab, which wasn't something that you chose. On the other hand, a lot of times, as you were thinking about new ways to do figures, you were discouraged by some of your mentors, who were concerned you were going down a road that wouldn't lead you anywhere.


Science is unpredictable, really. New discoveries are new, we don't know them yet. They're new things. I think if you look at what's happened during this century, all the big changes have been sudden and unexpected. Nobody expected the nucleus to give out much energy, for example. I know many people who argued against semiconductors for computers. And just before this century there were people saying anything heavier than air can't possibly fly. A balloon maybe, you put some light gas in it, but you can't expect anything heavier than air. Then along came the Wright brothers and there it was, and now an airplane became obvious. And so it was with the laser and with many things that have happened in science, and new things we don't yet envisage. Once we envision them clearly, why, then we may develop them.

Now, I think in the first place, a scientist has to try to understand things. Science is puzzle solving, but it's understanding also what puzzles other people have solved. We need to accumulate the information that other people have produced. Another scientist produces new information, which is then the property of everybody else. So you learn that and then you think about, well now, there are things we don't understand, and try to solve that puzzle. In addition, you want to talk with other people and argue with them. If you disagree with them, okay, then maybe that's good. If they think you're wrong that may be good, because it will make you think, and you should examine yourself carefully. Don't be too egotistical, examine yourself carefully; but if you think you're right, you stick to it. And that's happened many times with me.

In the case of the maser, for example, we were trying to build it at Columbia and Jim Gordon, a student of mine, was doing his thesis on it. He worked at it for a couple of years and two of the top professors in the department (I was a young professor then), the head of the department and the former head of the department -- he was a Nobel laureate -- came into my office and said, "Look, that's not going to work. You know it's not going to work, we know it's not going to work. You're wasting the university's money and you really ought to stop." Well, I told them simply, "No, I looked at it carefully. I think it has a reasonable chance." Well, they walked out kind of angrily, and they couldn't stop me. And so we kept going and in about three months it was working.

It was important that I had thought about it. It was important for them to question me, because that made me check it all over again. And when we got it working, they were friendly enough. One of them came around and told me, "Well, I guess I should realize you know more about what you're doing than I do."

Many times that happens to scientists. People will disagree with you, very eminent scientists may disagree with you. But it may be just over those things that are new that people haven't realized yet, and that they have to be wakened up. We all get set in our ideas if we're not careful. So you have to be independent enough. You have to listen to other people, but be independent. You have to be curious, think about things, explore things. And have good fun finding out something's new.

And as part of this you have to persevere, right? You are a navigator, explorer. You have to keep at it, listen to the criticism, but if necessary, change your course.

Yes, yes, that's right. The criticism may be right, and you want to think about that carefully. And if so, if you're going off in this direction you decide, well no, you'd better bear in that direction.

You think of the explorers of the American continent that came out. They didn't know what to expect, many of them. They would hit a dry desert they would have to walk through for days with no water. And high mountains, and so on; they didn't know what was beyond, but they had some confidence they'd find something, and eventually, of course, they found a lot of wonderful things out west.

Science is very similar: it is exploration. We have to be persistent, and we're going to fail sometimes. You just accept that, you fail. Actually, if you investigate something that might be true and you find clearly it's not true, that's a discovery, too, because you've understood now, "No, that isn't the case." And you've understood something that other people probably haven't understood before. So a failure in that sense is still good science. It may be more exciting to feel you're successful, but a failure in that sense, when you really understand something better, that's good science.

In your particular case, part of your contribution was to show the significance of the concepts and the ideas that you had been working with in the industrial lab and give it a new importance by redefining what it meant for what could be done. Is that fair?

Yes, I think so.

Another aspect that I would emphasize is that my experience in an industrial laboratory and with engineers was a very important part of my recognition of what might be done. Because physicists didn't have much to do with amplifiers and oscillators and so on, engineers did. Engineers didn't know quantum mechanics and atoms and molecules. The physicists knew atoms and molecules and quantum mechanics, but they had a kind of a set mind about what could be done and what couldn't be done, and they didn't understand the oscillators and amplifiers too well. They weren't terribly interested. And really, the field grew out of a marriage of physics and engineering, the marriage of quantum mechanics and electrical engineering, you might say. A marriage of light and electronics: the laser.

Many people, when the laser came along, said, "Oh, that's a very cute idea. That's nice, but it's a solution looking for a problem; what can it do? What's it going to solve for us?" It was so new they hadn't thought about what it could do. Now, from my viewpoint, I said, "Look, it marries optics and electronics. Both of those are very important. You marry those two fields and there are going to be lots of applications," and I could see some applications. I couldn't possibly see all of them. You can't ever. Science keeps evolving.

It was your curiosity, your quest for understanding, and not your sense of what finally would come out of all of these discoveries.

The reason I was trying to get short waves was to do science, find out more about molecules. I wasn't looking for an application. I wasn't thinking of a laser beam that would be a bright light or something. I wanted to find out more about molecules and I wanted to get shorter waves to study the molecules. Just basic work, not applied at all. But now look what's come out of it, all kinds of applications.

You should think about a research director or a political person who wants to donate some gifts, give some state money to have the right thing developed; would they say, "Well, now, I want a very bright light, so I'm going to give some money to somebody to study the interaction of microwaves and molecules"? No, it's completely out of the field. Or, it's a very important surgical tool, for the eyes especially, but in many other ways it's a very important medical tool. What doctor would say, "Well, I need a new surgical instrument, so I'm going to get somebody to study molecules and their interaction with microwaves"? They wouldn't possibly do that. And yet it's clear it grew out of that field.

In fact, there were three different people who more or less had this idea. Myself, and then there's Joe Weber at Maryland, and then there were a couple of Russians, [Nikolai] Basov and [Alexander] Prokhorov in Moscow.

This is the idea for the maser?

The idea for the maser, that's right. The basic idea for the laser too. The three different people who had the idea all worked in this field of microwaves and molecules. So it's clear it had to come out of that field, the right ideas coming together. And it's very important that we may think we know a lot, and we do, but when we know a lot we also get sort of fixed in our ideas. We go down a given track. We don't look off in a corner somewhere and suddenly find a whole new patch of things. When the maser came along and the laser, it was sort of like opening a door -- I didn't even know the door was there -- and going to a room, a fantastic room that I never dreamed might be there at all. You just get this little trail in the right direction and you lead into all this wonderful stuff. And unpredictable. But it's fun doing the exploring.

You say at one point, "I have tried to devote my energies to opening new fields with the intention of moving on to other things as soon as they start to become well established. I like to turn over new stones to see what is under them. It is the most fun for me to be on the fringes, exploring aspects that seem interesting to me but have not attracted the attention of others. Once a field is opened up and is successful, and once others are flocking to it, I feel my own efforts in it are no longer critical, and about that point I like to move on to something I think may be promising but overlooked."

Yes, I think that's more fun. Let's take the laser, for example. As soon as it really broke through and we had them, then all kinds of people started working on it, industry and so on. There were lots of people working on it. It was an interesting field and I worked at it for a few more years, but then I decided, well, there are plenty of people working on this. There are other things to be discovered that are being neglected, and so I went on to other things. And I characteristically have done that. I've changed fields about every ten to fifteen years. A field develops, lots of people are in it, it's going strong, why then I'd rather go off and look for something new.

Tell us a little about this.

Let's go back, now that we have a better understanding, to that moment in the park, that moment of discovery that many things followed from. What were your feelings at that moment as somebody who's just interested in understanding?

It's like a sudden revelation. A sudden revelation, an inspiration, a sudden revelation. On the one hand it seemed almost too good to be true. I wasn't sure it would ... I thought the principles said it would work. I wasn't sure whether we could really make one work, getting the right things together and so on, but I thought probably so. There were questions, but as well a great excitement, "Hey, this looks like a way of doing it." Later one might say -- I certainly said to myself -- "Why in the world wasn't this discovered before? There was no one idea that somebody didn't know, it was just a question of putting it all together and seeing what its importance was." And yes, that was the point, because it could have been discovered twenty years earlier. But even after I had the idea, many people thought, "Well, okay, it's kind of an interesting idea, but where is it going? It isn't going to do anything."

A lot of people came in my laboratory and saw we were trying to build this maser. They said, "Oh yes, well, a nice idea." But nobody else tried to build one. They didn't compete with us. They didn't think it was worthwhile, you see, worth the effort. But I thought I saw some possibilities there, and so when we got it going and showed what those possibilities were, very pure frequencies, very sensitive amplifiers, then everybody got excited and lots of people jumped into the field, and then it was a very busy field.

The same thing is true of the laser. Because the maser had been so successful, when I had the idea of the laser, as soon as I published it and made it public, then everybody got excited. They didn't have to wait until I built one. Somebody else built one first, Ted Maiman built the first laser, actually. Everybody jumped in the field trying to race to build one. And all the first lasers were then built in industry. The ideas came from academic fields, but a lot of the people who trained in those fields had gone into industry. And once industry saw it was useful, then they did a very good job. They could concentrate on it. Many of these things are built and done and further developed by industry now.

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