Interview: James D. Watson

James D. Watson has been a pivotal and enduring figure in the field of molecular biology since 1953, when he and Francis Crick sparked a revolution with their discovery of the helical structure of the DNA molecule. This research breakthrough has been described as the most important event in 20th-century biology, as profound in its implications as Charles Darwin's theory of natural selection a century earlier. Dr. Watson was only 25 years old when the now classic Watson-Crick paper, reporting their findings, was published in the scientific journal Nature.

In 1962, Dr. Watson was awarded a Nobel Prize along with his collaborators Francis Crick and Maurice Wilkins. Dr. Watson's best-selling book, The Double Helix (1968), is a personal and provocative account of the race for the double helix and illuminates the competitive side of science. Dr. Watson has also written the classic textbook in the field of molecular biology, Molecular Biology of the Gene, published in its fourth edition in 1987.

Since 1969, Dr. Watson has served as the director of Cold Spring Harbor Laboratory on Long Island, a research institution with more than a hundred scientists working on important problems in molecular biology. Cold Spring Harbor is also a center for the exchange of information, and each year thousands of scientists from all over the world gather there to attend symposia and summer courses.

In the following interview, Dr. Watson addresses many of the important topics considered in this unit and emphasizes how scientific progress is shaped by the introduction of new research techniques.

Dr. Watson, what initially stimulated your interest in biology?

As a boy growing up, I was very curious about animals. My hobby as a teenager was bird watching, and I was very interested in evolution. I was also interested in humans: where we came from, what our capabilities are, what limits us. I went to the University of Chicago, where I took a biology course my first year. I ended up getting a B.

When did you become interested in genetics?

By the time I was 15, I was aware of genetics: that there were discrete entities called genes, located on chromosomes, that determined the color of our hair and the color of our eyes. I had a long-term goal of trying to understand genes. By the time I got into graduate school, I realized that if you're going to understand genes, you've got to understand the simplest forms of life, the bacteria.

How do you define the gene?

I initially defined it as a discrete unit of DNA that produces a given protein product. But later, in 1977, we found that a given piece of DNA can give rise to several different protein products through processing of messenger RNA precursors.

You mentioned the importance of studying the bacteria. Another organism closely associated with the field of genetics throughout the 20th century is the fruit fly Drosophila. We also read in the press about important research that involves yeast, mice, and corn plants. How do geneticists and molecular biologists go about choosing which organism to work on?

It depends on what questions you're asking. Drosophila was the best organism for genetics from about 1910 to about 1940, and then almost everyone forgot about it. Now it's right back in the center of things, partly because its genetics are so well known. It may be the organism for understanding embryology.

So, you want as simple an organism as possible, but one that is complex enough to answer the questions you want to ask, right?

Yes. If you want to learn about the regulatory functions of genes in eukaryotic cells, for example, you should probably work on yeast. But yeast is never going to tell you how the nervous system works or how a complex organism develops. So if you're interested in the relationship between DNA and more complex phenomena like development, Drosophila is the organism to choose.

How do you explain the decline and subsequent reemergence of Drosophila as a model organism?

If someone had told me 20 years ago that he or she wanted to work on Drosophila, I'd have thought that he didn't have much sense, because it isn't a very good organism to do biochemistry on. If it weren't for the tricks we've learned relatively recently from recombinant DNA, no one in his right mind would work on Drosophila to answer biochemical questions. Now, with recombinant DNA techniques, you can take a Drosophila gene and get it to function in a bacterium. You can study the biochemistry of Drosophila in ways that would have been impossible prior to the development of these techniques.

What are the advantages of the mouse as a model organism?

One of the advantages is that if you understand the mouse, you might begin to understand many aspects of human biology. Ultimately, however, the questions that interest us most involve our own uniqueness. Why are we so extraordinary? And why is a mouse so much less interesting? Now, the mouse is a very challenging thing, but do I really care about those aspects that make a mouse? No! Absolutely not at all. Do I care about humans? Yes! Because no mouse was ever a Shakespeare or Beethoven or Einstein. Never will be. Never will realize its place in the universe.

The older I get, the more impressed I become with life, with how subtle and wonderful it is. It's all there, in some sense, because of what's in our DNA. We have evolved to the point where we have this extraordinary self-knowledge. And we are going to learn more about ourselves by studying our own DNA.

So, geneticists and molecular biologists work on a variety of model organisms, often with the long-term goal of finding applications to human biology. Yet problems like finding a cure for cancer are staggering in their complexity. Do such long-range objectives have a place in the research lab?

Scientists are people who are future oriented. They have to cross bridges that haven't been built. When you identify a scientific problem you want to solve, it often looks unsolvable in the short term and so you devise a plan of attack that might take many years. Now, a young person isn't very eager to get into a field in which the real answers will only appear after his or her death. So you've got to have some objectives that are solvable within a couple of years. You need guideposts, short-term objectives that give you a feeling of success and self-confidence. You have to have a mixture of short- and long-term objectives. In many cases, something unexpected turns up and you don't solve the problem the way you think you would have solved it to start with. But you always have to have a battle plan. If one doesn't work, you can go on to another one.

Isn't that part of the excitement of science: that you don't know exactly what you're going to find, and when you do, it brings up another fifty questions?

Yes. Many people have occupations where they know what to do, where they apply preexisting laws in some practical way. Civil engineering, for instance, is an occupation where you essentially learn a trade. You apply the knowledge of the past so that you don't make mistakes in the future. Many forms of science are different.

How important is a historical perspective in science?

When you first learn science, you want to know the facts. You want to know the laws of Mendel, though you don't really care who Mendel was. Later, if you go on to do research, it's quite important to know the history of your field. It's part of your education to know what went before, because you sometimes see where people made mistakes. So you want to know not only what your teacher's objective was but also what his teacher's objective was. Research students who know the past have a decided advantage over those who don't.

I think everyone reading this book will have learned in high school about Watson and Crick working out the double helix. Did this breakthrough conform to the kind of long-term planning you've described?

Not really. In 1953 we knew where we wanted to go, but it seemed a very, very long distance. The discovery of the structure of DNA was actually a glowing exception to the rule that things turn out to be more complex than expected. Everything was much simpler than people thought it would be.

Where did your investigations lead you after 1953?

After we found out that DNA was a double helix, we could formulate many questions in more precise ways. The first major question was, How does the DNA molecule replicate? which is the same as asking, How does one chromosome become two? We first thought the chromosome might be a linear collection of DNA molecules. In time we realized that the chromosome was one very, very long DNA molecule that had signals encoded into it. These signals, in a sense, said, "Here's the start of a gene, here's the end of a gene, here's the start of a new gene," and so on.

So how does this long DNA molecule duplicate itself? From the moment we saw the structure of DNA, with its two intertwined chains of complementary shape, we thought we knew the answer. One shape could serve as a mold for the formation of the second. And that turned out to be right. This was proven with 99% certainty by experiments done at Cal Tech by Meselson and Stahl in the late 1950s.

The second major question was, How does DNA control cellular activity? If the gene is a long message written with a 4-letter alphabet, how can that determine the structure of proteins, which are made up of 20 different amino acids? So we had the problem of translating a message written in a 4-letter alphabet into a final message in a 20-letter alphabet. We knew, however, that DNA didn't make protein directly. There was an intermediate. Already in 1953 we began to focus on RNA, because we thought it was the direct intermediate between DNA and proteins. Initially I began to study the structure of RNA but soon found that we couldn't proceed in the same way that led to our success with DNA. RNA did not give a solvable X-ray diffraction pattern.

A completely different approach was necessary, and some of us began to concentrate on biochemistry, on the enzymatic reactions occurring in cells. That was a period of intense investigation culminating in the elucidation of what we now call the genetic code. And by 1966 the genetic code was an established fact being taught at the college level.

What changes have you seen in the research atmosphere in molecular biology since you started out?

First, there are many more people doing science, so it's harder to feel your uniqueness. In 1947 there were certainly fewer than 150 to 200 people who seriously thought that DNA might be the most important thing to work on. And even though a number of people thought it might be important, fewer still were actually following this sort of hunch. So I always thought I was working in a universe of somewhere between 5 and 25 people. Now if you put all the people in the world interested in DNA together, you could fill a baseball stadium. But there are also many more problems to work on: DNA and genetic birth defects, DNA and cancer, DNA and aging, DNA and producing better plants.

What area of research do you feel will have the most pervasive influence on solving these types of problems?

The central problem that faces biology is development: How do you change from a simple fertilized egg into a complex, multicellular organism? All the instructions for this have to be programmed in DNA. There won't be one answer to this question; there will be many, many different answers, and many people are focusing on different aspects of it. I think the most successful people are the ones studying simple organisms who are trying to understand the genetic switch; that is, what causes development to go in one direction rather than another at the molecular level?

We know that DNA contains a blueprint with all the instructions necessary for the development of an entire organism. My students sometimes ask me if it might someday be possible to recreate a woolly mammoth, for example, if we had the entire nucleotide sequence of the extinct creature's DNA. How would you respond to their question?

I'd say that it's a sillier objective than the belief that we could successfully fight Star Wars. The idea is so removed from reality that anyone who would think that way would be either stupid or mad. It's science fiction. There are so many steps, I have no idea how you'd ever get there.

This whole issue of the molecular basis of development raises another question. There seems to be a historic division, reflected in the organization of biology departments at many universities, between molecular biology and organismal biology. Do you see more opportunities for collaboration these days?

Yes. Before the advent of molecular biology, we didn't have the ability to think in terms of molecules. And now we do. Modern molecular biology has provided many tools that have been useful to organismal biologists. For example, it turns out that comparisons of DNA in living organisms have been extremely useful to biologists studying evolution. They're asking questions like, How different are we from the chimpanzee at the level of our genes? And accounting for these differences helps them to estimate how many millions of years ago the line that gave rise to humans diverged from the line that gave rise to chimps.

Earlier, you mentioned your interest in bird watching. Do you ever regret not pursuing a career in some field of organismal biology?

Evolution has always been an extraordinarily interesting field to me, and if I had the time, I would like to put together a book on evolution aimed at an audience of molecular biologists. But to be honest, I don't think the people who went into evolutionary biology in the early 1950s have had as interesting a life as I've had in terms of learning new things. To me, it's not as exciting a field as it must have been at the turn of the century, when Mendel's laws were rediscovered and biologists began to interpret evolution in terms of the rules of genetics. Now, if I had been born in 1880, I probably would have been dominated by Darwin. I would have wanted to travel all around the world to find out how evolution occurred. But I wouldn't get much excitement now, let's say, if I were in New Guinea observing extraordinary birds, because I wouldn't be doing anything very new. If I'd been there 100 years ago, I would have been an explorer.

I'd like to ask you a couple of questions on subjects that are receiving a lot of attention in the popular press. You mentioned earlier the importance of recombinant DNA techniques in helping us to understand the biochemistry of Drosophila. In what ways are these techniques contributing to our understanding of basic biological mechanisms?

Recombinant DNA has given us many important tools. Its methods have speeded things up so that problems that were effectively unsolvable have become, in some cases, easy to solve. The whole field of immunology has been drastically transformed by recombinant DNA technology. The most important breakthrough conceptually was in understanding the genetic basis of the immune response. We discovered that the DNA for antibodies was being shuffled around. Through the rearrangement of different segments of DNA, you get the enormous diversity of genetic information necessary to produce the extraordinary number of different antibody molecules. Also, we're beginning to get new insights into the nature of cancer.

What's the most exciting thing going on now in cancer research, in your opinion?

Before, in studying cancer, we never knew the ultimate basis of the defect. Now we know it's changes at the level of DNA; they're finding pieces of DNA whose misfunction makes a cell cancerous. We guessed that 30 years ago, but without the techniques of recombinant DNA, there was no way to get the pieces of DNA out. Now we can isolate those pieces of DNA. So you go to the ultimate cause, which is a change in DNA, and try to figure out why a mutated gene makes a cell cancerous. This approach has application to other diseases, such as muscular dystrophy and sickle-cell anemia.

What do you think the possibilities are, realistically, for cures for people afflicted with these types of diseases?

Some bright, intelligent, serious people think they're going to succeed in finding cures. I think most scientists have a feeling that the more knowledge we have, the better able we will be to deal with the precise problems. We certainly have an example of that now in the case of AIDS. Twenty years ago, we wouldn't have been able to pinpoint the cause. Now that we understand that a group of viruses called retroviruses is involved and that they have this special enzyme called reverse transcriptase, we can begin to think about preventing the replication of this virus. No one has done it yet, but it's something we've talked about in a scientific fashion, rather than just wringing our hands and saying, Heaven help us! Now we can hope that our brains will help us.

You were only 25 years old at the time you and Francis Crick made your discovery. If you were 25 today, what particular problem would you choose to work on?

I'd want to work on how genes determine the development of the human brain. This problem is very much related to the whole issue of the molecular basis of development. We don't really know what the brain is, in a functional sense, any more than we knew what DNA was back in 1953. A lot of people say it's a series of parts, and this part has to do with hearing, and this part has to do with bodily movement, and so on. But if you get down, precisely, to what the brain is, we're totally in the dark. Neurobiology has an enormous future because there are tools now that allow you to do things you couldn't do 50 years ago. This field is likely to challenge people for many years.

Finally, what would be your advice to an undergraduate student who may be contemplating a career in the sciences?

Pick your objective first, and then see what you have to learn to reach your objective. If you want to do science, you should come into contact with people who do science, so you can see how they behave, see how they think, because at some stage you've got to test yourself against them. You've got to be able to ask them intelligent questions, and if they ask you questions, to reply. If you want to become a great tennis player, how are you going to know where you stand if you never play with other tennis players? Ambition should be focused. If you think you don't have to go where the action is, that's a mistake.

When it comes to choosing a specific area to focus on, you should pick something that will interest other people. (That doesn't necessarily mean your mother; she will be interested in anything you do!) In the final analysis, one way of judging whether something is important or not is whether it interests other people. That's what you go to school for and that's what you read good books for: to develop a perspective, to be able to say what the key problems are.

©2005 Pearson Education, Inc., publishing as Benjamin Cummings