Interview transcript

Dr Baltimore, you have been an active scientist for close to 40 years. How did it all started; how did you get into science?

David Baltimore: I got into science really because of my mother. My mother was an experimental psychologist and she arranged, when I was in high school, for me to go to the Jackson Lab and Bar Harbor, Maine. I had the opportunity to do research for the summer in mass genetics and it was fabulous, and I never looked back so it was really after my junior year in high school that I was determined to be an experimental scientist, biologist, and through college and graduate school there was never any question that that was what I was going to do.

Was there any teacher that inspired you?

David Baltimore: It was really the people at Jackson Lab who inspired me. My high school teachers, bless their hearts, were terrible, particularly biology teacher was the worst. But the scientists there, Timmy Russell, Willy Silvers, Don Bailey, Charity Weymouth, were just fabulous people. Many of them were founders of contemporary mass genetics and for high school students to work with people like that is a very rare opportunity but they were so wonderful and made it so clear how exciting it was to do science.

What happened after Jackson Laboratory, the summer experience?

David Baltimore: I went back to high school and then I graduated and went to Swarthmore College and at Swarthmore there were many wonderful people but none of them were involved in what I would call contemporary research and so none of them were role models for me. I ended up teaching molecular biology when I was in college because I knew more than any in the faculty did, I just learned it from seminars. One summer programme I was at Cold Spring Harbor one summer and worked with George Streisinger. George was one of the central members of the Phage Group, very much of a sciency scientist, not well known outside of the field and a terrific man, superb man, and I worked experimentally with him for the summer and that was a great experience, and he was always somebody I looked up to.

You got also in contact with Salvador Luria at an early stage.

David Baltimore: At Cold Spring Harbour that summer, which was the summer after my junior year of college, a couple of people came, everybody used to come to Cold Spring Harbor for the summers, Delbrück and Luria and Leventhal and all the central people in the phage school.

These are in the late 1950s.

David Baltimore: This is now the summer of 1959, right, and Luria came and Leventhal. Both of them had recently become faculty members at MIT and they were starting one of the very first departments in molecular biology. In 1959 if you’d become interested in molecular biology, there were really only three places to go, to MIT, which was just starting out, to Rockefeller, which of course had been the centre of medical research in the United States for a long time, or Caltech, where Max Delbrück had the great school of molecular biology that generated the whole phage focus. The idea of going to Caltech oddly enough, never entered my head, the thought of going to California was just further away than I could imagine and although my previously good friend, already good friend, Howard Temin had done that, had left Swarthmore and gone to Caltech, but I couldn’t even think of that. So, I went to MIT, and it was really because I had met Luria that summer. He and Leventhal recognised that I was able to do these things pretty easily and that I had a good experimental sense and that I wanted to do the right things, so they asked me to come to MIT and that was the only place I had for graduate school so I went there.

So rather than starting to work on phages, you decided to go in a totally different direction, that of the animal virus.

David Baltimore: That’s right.

What made you make this decision?

David Baltimore: I guess I had the feeling that the heyday of phage research was over, that phage had done for molecular biology what it was going to do and that in my career which after all wasn’t going to start as an independent investigator for another 5–10 years, that I should be looking somewhere else and I didn’t know where to look and so I took what was the most, the easiest sort of analogue or analogy. The analogy was if phage had been so important for working out the molecular biology of bacteria, animal viruses should be able to do the same thing for animal cells. I guess what that means is, although I didn’t think about it a lot, that I had already decided what I wanted to work on was the molecular biology of animal cells. I don’t know why, but I did and I saw animals viruses as a probe of that and so I went to Leventhal who I was doing some experiments with and I said, What do you think of that idea? and he said, You know, I’ve wondered that myself, he said. So that was helpful but didn’t get me anywhere so I went to Luria who was everybody’s greatest teacher and I said the same thing and he said, That’s an interesting question, why don’t you spend the summer investigating it. I’ll arrange for you to work with a young animal virus person, Phil Marcus at Albert Einstein [Medical College] and to take the animal virus course at Cold Spring Harbor.

I did that after my first year at graduate school and it was a revelation because there was just an enormous amount to be done and nobody was doing it. And so I came back particularly from the Cold Spring Harbor experience and said, Yes, this is what I want to do, but the man I want to do it with is Richard Franklin, who was the guy who was teaching the animal virus course that summer and he was at Rockefeller. So Luria arranged to help me transfer to Rockefeller which was a wonderful thing since he really had very few students at MIT in, as registered into microbiology because it just wasn’t something everybody was doing in 1960. And so, I transferred to Rockefeller and did my thesis in two years there and exactly what I suspected was true, was true. That is there was an enormous … to be done and every time you did an experiment you discovered something. I published lots of papers and had a very good time.

The reason that one could start to address these questions for animal viruses was probably the development of the cell culturing techniques that made possible to make experimentations in the lab.

David Baltimore: There were many different strains of development that lead to that moment being so opportune. One was cell culture. Harry Eagle developing a medium that you could use and learning how to manipulate healer cells and other cells. He was central and of course Dulbecco invoked having developed a plaque assay for animal viruses so you could do quite a … of animal virology. Now that was only a couple of years before that the assays had been developed. That’s one of the things I discovered in Cold Spring Harbor was the plaque assays. Rubin and Temin’s work in the development of the quantity of assays for cell transformation, the focus-forming assays from the sarcoma virus that was also a very important strain, but for me, interested in molecular biology, one of the main things was biochemistry. It was the work of Kornberg with DNA polymerase basically and then lots of other people doing lots of other things, Ochoa with polynucleotide phosphorylase and whatever, but the DNA preliminaries was a key. It’s interesting, if you read what people were saying in the mid-50s about DNA when they were just trying to figure out whether DNA encodes proteins and how DNA replication occurs, they didn’t know what the precursors for DNA were. They really didn’t understand DNA synthesis, never mind the sort of geometry of replication, they didn’t understand the basic formation of the bond. Kornberg’s working out that the triphosphate was the precursor and that you could label with phosphate or with iridium the basis and getting corporation was a key.

One of the things that a lot of my thesis work was involved with was in vitro synthesis of poliovirus and Mengovirus RNA, an inhibition of RNA polymerase. Those things all followed on the models of Kornberg’s school basically, although the first … work was actually done by a guy in Chicago named Sam Wise. And then came radiography, radiography’s a very important tool at that point and Richard Franklin was one of the great exponents of that. That’s one of the things I had learned at Cold Spring Harbor and that showed us that viruses grew in the cytoplasm and cells made the RNA in the nucleus. You know, it wasn’t even clear then that all RNA was made in the nucleus, and I actually did some of the best experiments to show that using very rapid pulses in cells and autoradiography to show that all of the grains were in the nucleus. All the synthesis was going on in the nucleus, but if you did the same thing in a virus infected cell all the grains were in the cytoplasm.

So rather than picking a DNA virus that was … DNA was the hot stuff in those days, you focused on the RNA virus, the Mengo- and the poliovirus and then followed the RNA dependent RNA polymerase. What did that mean to you?

David Baltimore: Why did I do it that way? Really only because that’s what Richard Franklin worked on. It was not a conscious decision that RNA was more important or more interesting than DNA. In fact, in retrospect it was kind of stupid to do that although it worked out very well and got me in a new direction, but if I was really interested, I should have focused on DNA virus but then Richard didn’t do that, what he worked on was Mengo at the time and some with flu virus, most all, almost all RNA viruses. So that’s what I did, and I always figured I could do something else later if I wanted.

At some point you moved to MIT and then, based on your experience with the picornaviruses the polio and the Mengo you also looked for RNA polymerases in other viruses. How do you come about to do that, to expand to other viruses?

David Baltimore: It was not, it wasn’t a direct line, I had been doing work on the polio and Mengo polymerases at Rockefeller for my thesis and then when I left there and went to the Salk Institute I was actually involved more in protein synthesis and in showing the polyprotein was made and the important role of protein cleavage in the formation of viral proteins. When I came back to MIT in 1968, Alice Huang, then my post doc, later my wife, soon to be my wife, she was working on polio. She was trying to get some experience with the kinds of work that we had learned how to do over those years but she actually … Her first love was the vesicular stomatitis virus so she and I talked one day about what she was going to do in the future, and I said, Well, you know, it would be fun to work on a different virus. I’d been working on picornaviruses now for most of 10 years and that a lipid virus that had a whole different history would be interesting to start on. She of course knew how to deal with it and had wonderful stocks and worked out a lot of the biology interference which was necessary otherwise you’d spend your life studying interference, not the virus. We said, Let’s do that, and a student joined us, Martin Stanford, and we began to look at the virus.

At that point we were doing some hybridisation so we simply asked did the virus look like polio that is, did it have messenger RNA in the virus particle and quickly we were able to show that the RNA in the virus particle was not the messenger RNA, we didn’t find it on polysomes and what was the messenger RNA was the other strand and what the cell filled up with was the other strand, so these were clearly negative strained viruses. In fact we named them that because they had the anti-sense RNA not the sense RNA in the virus particle. But that then presented a puzzle because if a virus has within it anti-sense RNA, senseless RNA really, and that goes into the cell it can’t code for anything so there’s no way for the infection to get started. That puzzle lead me just wonder whether there wasn’t a polymerase in the virus particle that would get the whole infection started by copying the senseless strand and the anti-sense strand into sense RNA. Again I had all this background in biochemistry, looking for something like that was trivial for me, and so we just made some virus and opened them up with detergent and assayed it for RNA polymerase activity and it was … It went off the charts, that’s one of the easiest enzymes to assay that you can find. We were lucky we chose the right virus, I mean we were lucky that virus chose us, I guess. So that was fine and we published that.

And now we are in 1970.

David Baltimore: And now we are, yes, that was published in early 1970 I think, or maybe in the later, mid-1970, was finished in early 1970. And I started thinking about what other viruses you could study and find the same thing that is, you know ‘Hershey heaven’ – can I do the experiment over and over again and find new things. We tried viruses that looked like vesicular stomatitis virus, that is Newcastle disease virus and influenza virus. Newcastle disease virus, that was a polymerase, we published that with Mike Brett. Influenza virus, there was no polymerase activity, or there was just, I can’t remember, maybe there was a hint of activity but it was very low, and it was very hard to work with so we sort of gave up on it. I had been working on flu years before that, looking for … Showing that flu is acting on mice insensitive which is very strange, so flu was always a puzzle and now we know that flu is a puzzle, and we know why and it’s just much more difficult than these other viruses.

So now the stage was set for the real discovery.

David Baltimore: Now the stage was set. In the early 1970 one of the viruses I focused on was RNA tumour viruses, then called RNA tumour viruses. Rous sarcoma virus and murine leukaemia virus, very interesting viruses, very little known about them. They had RNA in them, very hard to grow, very hard to do any molecular biology and almost nothing known about them. I said, Well, let’s assay them, maybe they have a polymerase and of course I was very aware of the background of Howard Temin’s work for 10 years which had lead him to suggest that there was a DNA intermediate in the growth of these RNA viruses and that was an intriguing idea but it’s not that there was no support for it, there was almost anti-support for it. The experiments that had been done to test it were really very poor and came out of it, great poorly, didn’t work well. I was aware of that and said, Well, maybe there’s DNA polymerase in those viruses and that of course would explain everything Howard had been talking about and be very dramatic, wonderful. To do that I got in touch with some friends of mine who worked on these viruses and said, Is there any way I can get some material, because I wasn’t going to try to grow them, they were impossible to think about for me at that point.

Two people were helpful, Peter Vogt, who sent me a preparation of Rous sarcoma virus and George Todaro, who put me in touch with a group at NIH that was storing away enormous amounts of virus and they didn’t know why. They’d had a contract to do it and somebody thought it was a good idea to have it, it was in the freezer, and I called them and I said, Would you send me some, they said, We’d love to send you some. I don’t know that they’d ever had a request before for any of this material, How much would you like? I said, I don’t know, what kind of units do you measure it in? and they said, Millilitres. How many millilitres would you like? I said, What’s in a millilitre? They said, We don’t know. They didn’t have a biological measure, they didn’t have a chemical measure, they just had a protocol and it made millilitres and they froze those away and it was a contract firm, they didn’t know what was in there. But they said, It’s worth a lot of money. I said, Why don’t you send me … I don’t know, I can’t remember what I said … 100 millilitres? They said, Oh fine, we’ll do that, shall we send it by courier? I said, Is it frozen isn’t it, why don’t you just pack it up and send it? They said, It’s worth a lot of money. I never found out how much money it was supposed to be worth, but this contract was a very rich contract. They were spending millions of dollars on this stuff so this was certainly tens of thousands dollars worth of virus. But Vogt’s virus came first and the Rous sarcoma virus. I said, I’m going to do the likely experiment, so I looked for the same kind of RNA polymerase that I’d discovered previously in VSV and elsewhere and there was nothing there.

It was a good clean experiment and that was good virus and I knew the experiment didn’t work. But I had very little left after that because he hadn’t sent me much, so I left that frozen away and the virus came from NIH and there was these little millilitres of milky stuff. I put some in a test tube and now I said, I’ll assay for DNA polymerase and again I knew how to do that, I actually had been a post doc working on DNA polymerase, so I’d purified the polymerase, I knew all about them. And I got a hint of activity. One of these things that’s just enough to keep you doing experiments, but not enough so you know if it’s real or not. I just did something very simple which I took it and I centrifuged it for a while and took the pellet and re-suspended it in ten-fold concentrated and put that in the test tube the next day and it went off scale and I knew I had it. And then it was a matter of doing some control experiments showing it was rather nucleus sensitive, acting on mice and resistant and things like that, that indicated that it was RNA being copied, sorry, it was DNA being copied from RNA, not from DNA, not from anywhere else and we published it.

At the same time without your knowing I guess, Howard Temin was having exactly the same problem in Wisconsin and you published the papers back to back. How did you get to know about each other?

David Baltimore: He had a post doc, Mr Towney, who was working … Howard himself was definitely not a biochemist but Mr Towney was, and Mr Towney was working on this virus, Rous sarcoma virus, and I didn’t know that, I’d never heard of Mr Towney. I had not been in contact with Howard for a number of years, just hadn’t run into him, but I knew he’d be interested, so the moment that I had the data and was in the process of writing it up I called him to tell him, because I just knew he’d be interested. He then told me that he was working on the same thing and he also had data. I said, Well, let’s publish it together. I had already, I think maybe I had submitted the paper that day, so he quickly got his stuff together and submitted it about 10 days later and Nature did not take long to publish it.

Although for you the discovery of reverse transcriptase did not come as a real big surprise because you had anticipated that and that … to also for Howard Temin. The rest of the world were taken not by surprise, but even it was shocking news, because the centre of dogma at the time was that genetic information could only flow from DNA via RNA to protein, and now you went through against the central dogma. Was that immediately accepted by the scientific community?

David Baltimore: It was accepted and it was accepted largely because two of us had made the discovery, I think if one of us had made the discovery it would have taken a lot longer before people took it seriously and because Saul Spielman upon hearing about this went back to the laboratory and immediately got his people doing the experiment because he had wanted to find something like this but hadn’t really done the right experiment and he was able to reproduce it in no time at all. I don’t think there was anybody within a week or two, I don’t think there was anybody who doubted that the experiments were reproducible and correct. People could have worried about the meaning of the experiment because we had not really demonstrated what people thought we had demonstrated. And we said that. What we had demonstrated was that there was a polymerase in the virion in the virus particle that could copy RNA into DNA. If you set up the Kornberg polymerase correctly it will copy RNA to DNA. It could have been a DNA polymerase that usually copies DNA but that happened to copy RNA was a contaminant of the virus particle. That’s one of many hypotheses, because we had no genetic evidence that this was critical, we didn’t even know it was encoded by the virus at the time, there’s no way to know that. We certainly didn’t know that the DNA that was being made, although hybridised to the RNA so we knew it was a real copy, we didn’t know it had biologic abilities, that it was a real intermediate in the growth of the virus.

On the other hand, I must say everybody accepted our evidence as saying that and it’s a very interesting story in the sort of history of ideas, why a certain kind of experiment captures the community’s fancy and they believe it and believe all it’s implications right away even though, and the investigators may understand, should understand the limitations of it, people won’t think about it. Other kinds of experiments for one reason or another, all everybody thinks about is the limitations and they never think about … They won’t take this as the answer. I can think of two examples like that, one was the Avery experiments that showed that DNA was the genetic material, that was 1944 and yet most of the scientific community didn’t believe that until 1952 when Hershey and Chase did an experiment that was certainly no better and arguably a lot worse than the Avery experiment. Why was one experiment accepted and not the other, is the time, is the idea right, or was it the nature of the experiment? I think it’s the nature of the experiment and I could talk about what it is, but I don’t really know what the nature is that’s so important.

Another example was, and that may have been pure stubbornness, when the Watson–Crick model was published. The Watson-Crick model implied that these intertwined strands of DNA colour pairing are duplicated and the best minds of the scientific community, Allbrook, Leventhal, others at the time, focused on the difficulty of imagining that you could unwind the strands, that was the big question. There are many many papers published about the difficulty of unwinding the strands and actually Leventhal published the only sensible article about it in which he said it’s not a big difficulty, because he actually calculated the forces involved. But that was the generation of the Meselson-Stahl experiments. The Meselson-Stahl experiment … There’s a whole book about this that I’ve just been reading. Meselson was very careful to say that his work only showed that the nitrogen in DNA was semiconservatively distributed during DNA synthesis, but the scientific community immediately said that the unwinding problem is not a big problem, clearly that’s how DNA works, done. It was the years later before it was really proven that that’s how it worked. Why was the Meselson-Stahl experiment so influential and yet really limited in what it said. I don’t know. Anyway, our experiment was very influential and the world was very comfortable right away, but it was really hill and hell over. A pair of Czech scientists who a number of years later showed that the DNA intermediate that you can get from cells were infectious DNA that proved that there was a DNA intermediate. We didn’t prove it.

The Nobel committee and assembly were taken by your discovery …

David Baltimore: That’s good.

… and you were awarded the prize say just five years afterwards, in 1975, together with Howard Temin for the discovery of a reverse transcriptase. That’s an unusually short period for the assembly to be convinced of the impact of the discovery. Could you comment on the downstream effects of your discovery, the role of reverse transcriptase in biomedical research after that.

David Baltimore: I think the Nobel assembly was responding to one thing which was that our discovery of reverse transcriptase, whatever it said about the biology of the virus, provided the technology for working with retro viruses and turned an intractable viral system into an easy manipulable viral system because you had available of biochemistry to use. You could find out what the genes were, you could find out how the replication worked, you could uncover all of its secrets and ultimately because you could then find oncogenes using the copies of the RNA as probes. I think by 1975 that was eminently clear and probably, well certainly rarely in history have there been so many papers published that followed from an initial observation as there were published in the cancer research literature following our discovery. Cancer is the thing that frightens people most in the whole medical world and was at that point a virtually intractable disease, it’s still a very difficult disease, so a major step forward in cancer research was something that, in a sense it’s not surprising that the Nobel Assembly responded and responded to quickly and it was real. I don’t take credit for the fact that our observations lead to that, it was just that that turned out to be the bottle neck and then suddenly everything opened up. I think that’s what they were responding to.

Two other things happened soon thereafter but they weren’t clear in 1975. One was that we had also opened up biotechnology and we didn’t know that, but a year or two after we discovered the polymerase, we learned how to make enough of it, we learned how to assay it with exogenous templates, not just what was in the virus, turned out it purified easily. Then /- – -/ working in my laboratory as well as somebody working with Phil Leder showed that you could copy globin messenger RNA with it and that was in terms of bio technology one of the most important discoveries that was made, because it opened up the whole ability to capture the information in messenger RNAs as DNA and allowed you to use what then became cloning technology but of course that was only after 1974, 1975. You could use cloning technology to insert genes and detectors and to manipulate them and so that was a really central technology. But it wasn’t so obvious by -75 that that was true.

The third thing was obviously only done in 1982-83 and that was the discovery of HIV, because HIV is a retro virus like the ones we’d been working on and was in fact discovered by its reverse transcriptase activity, that was a tremendous downstream advantage. Had HIV been discovered in 1970 rather than 1980, nobody would have known how to look for it, because we wouldn’t have had that information. If it were discovered in 1960, ten years before reverse transcriptase. The world would have been a terrible place for that because it was already getting to be a terrible place by 1982 because of fear. It’s the kind of thing we now see with mad cow disease, when you don’t know the biology of a situation people get terrified about where the disease might come from and how it might affect them and they stop eating meat even though the meat of the animals probably doesn’t have any chance to hurt them. This stopped sex and dealt with a transmission of a basically sexual disease. It was a terrible time for two or three years there when we didn’t know it was a virus and every hypothesis you could imagine was being suggested. It was an immune response to semen, was a classic thought. It never occurred to me but some other people, so yes, the discovery had lots of downstream impact and that was enormously gratifying. It continues to be, we just sequenced the genome, the human genome, and it turns out to be on the order of 50% of the human genome comes about by reverse transcription so it’s not exactly a small mechanism in biology.

By the so-called retrotransposons.

David Baltimore: The retrotransposons, but also all of the repeated elements, the halo sequences in all, all come about by reverse transcription, never mind that the ends of all the chromosomes come about by reverse transcription in telomerase, so lots of things came.

When you did the discovery in 1970 you were only 32 years old.

David Baltimore: I felt like an old man by then.

And you were 37 when you got the prize. The general idea is that once you get the Nobel Prize your scientific career is almost over and it’s deleterious for your future research. How did the prize affect you?

David Baltimore: It affected me in lots of ways, I became a sort of semi-public figure, but I tried hard not to live up to the prize, that is to somehow change the way I lived because I was a Nobel Prize winner, and most of the time I could manage to live without thinking about it. I just continued to do science the way I wanted to do science and have done so since. The year I won the prize, 1075, I was on sabbatical in New York with a clear desire to change the orientation of the science I was doing. The reason for that goes right back to where we began this, that cloning technology had come along and it was now clear that we were going to be able to do with animal cells what we had previously only been able to do with viruses or with bacterial cells, because we could take out the genes one by one and clone them and characterise them and put them in bacteria and deal with them that way. I said to myself this is the time to move to a mammalian cell system that would enable me to look at genes in mammalian cells rather than genes of viruses. The system that I really wanted to work on was the immune system and I should have gone to a laboratory where I could do that, but most of the laboratories where I could do that were either far away or I didn’t want to be there. I instead went to Jim Darnell’s laboratory in New York at Rockefeller, partly because it was comfortable for me, partly because my parents were in New York and partly because the important thing was to get away. The Nobel Prize followed me and so I didn’t have the nice quiet year that I expected to have, but I did manage one way or another to learn enough and think enough and talk to enough people to decide that I could move into immunology and use the background that I had effectively in immunology. I’d always had immunology in my sights ever since I was at the Salk Institute because at the Salk Institute I’d become very friendly with a number of immunologists particularly Martin Weigert and Mel Cohn and they were extremely clear thinkers and they had oriented my thinking about immunology in a very, what turned out to be very productive and what seemed to be then a very precise way and it was a focus on, again the molecular mechanisms on, gene rearrangements on somatic mutation and … so that’s in fact what I did.

This time in the mid 1970s was also a very critical time for the development of recombinant DNA technology, I think -75 was a critical year. You together with some prominent scientists raised the warning finger and you convened a meeting in Asilomar to discuss what the implications of the new recombinant DNA technology could be and the risks involved. That also led to a moratorium of gene cloning or recombinant DNA work in Cambridge, Harvard and MIT. Could you tell a little about why you took that step and whether that was a thing you would re-do if you would re-live it.

David Baltimore: There was a presentation at a Gordon conference in the summer of 197-, I think it’s -74 it may be -73, that Maxine Singer had been involved, I think she’d organised the meeting and she wrote a letter to the National Academy of Sciences along with the other co-organiser of the meeting Dieter Söll saying that at this meeting it had been announced that it was possible to put together pieces of DNA from different sources and re-insert them into bacteria and get them to be maintained and that was the start of recombinant DNA technology. Anybody could look downstream and see that this was going to be a dominant technology of molecular biology from then on. But there were a lot of concerns and there were some very particular ones that made sense to me. One was that you could spread animal viruses if you tried to put the whole copy of an animal virus into a bacterium, because the bacteria could be a source of the virus and that this was a sort of unnatural system of spread. Same thing was that you could spread antibiotic resistance because you could put genes for antibiotic resistance into bacteria in the lab in this cloning way and then they would spread to other places. And there were some other concerns that we had that were, I think, pretty precisely focused. Then there was some very vague general concern about whether we really knew what we were doing if we were going to put genes from any source into any other animal or plant or bacteria.

We didn’t know how to respond to this concern so the first thing we did was that a small group of senior people got together to talk about it. Actually, the letter was sent to the National Academy, the National Academy called Paul Berg and said, Paul, help, what do we do about this? Paul called me and I said, Let’s have a meeting. We all got together at MIT actually, in the cancer centre, on the fifth-floor conference room in the cancer centre and talked for a day about this. In the end we decided that first of all this is a problem that, this is a situation that if it became a real problem was going to get out of hand very rapidly. Unless we stopped what people were doing and had a breather and thought about it for a while, we were just going to march ahead without thinking, so we said this is a situation which we needed to monitor. We called this form moratorium in the sign of the community, we didn’t have any status to do this, but we did it and we wrote a letter that was published in PNAS and in Science magazine signed by Paul Berg and me and Jim Watson and Norton Zinder and a whole group of people. We brought that letter to the National Academy as a response to their concern, and it was adopted by the National Academy as an appropriate action. As far as I know it was absolutely observed by everybody in the community and it said, Let’s not do certain kinds of experiments – and it was the kinds that I talked about, antibiotic resistance, genes and virus genomes and that sort of thing – and let’s get up some kind of regulatory framework around this.

The big question that none of us knew enough about, it was partly because of the people who were there, was what’s the natural history of virus, of bacteria that we grow in the laboratory. Some of us felt that probably anything you grow in the laboratory is so feeble as an organism and is so full of genes that you put in there and mutations you put in there that it couldn’t possibly grow in nature. But other people said, How do you know that’s true? and we didn’t and How do you know that it couldn’t share it’s genetic material with some other organism in nature and so maybe it can’t grow but it can transform another or make with another organism? and we didn’t know. We felt there were a lot of questions there and there were some people who knew about this, who had worked more on unnatural situations. We said, Let’s all get together and have a meeting and talk about the science that underlies the kinds of issues that concerned us, and ask ourselves are these issues? We put together an international meeting which was held the next year at Asilomar, known as Asilomar 2, because we had all been together concerned about another set of biological safety issues and we had Asilomar 1 a couple of years before that. The recommendations that came out of Asilomar 2 was that we should keep the moratorium in place effectively – we didn’t like the word moratorium but that’s what it was – but find a way of dealing with the question serially and reducing the kinds of containment that were necessary to do these experiments or establishment containment and then reduce over time, which meant two things. We needed a national panel to oversee this on a continuing basis and that was established as the recombinant DNA advisory committee of the NIH and that we had at all costs avoid legislation because as soon as there was legislation, and there was a lot of public interest at that time, it was going to be frozen in stone and almost impossible to reverse because once you put in some regulatory framework and legislation, getting it out of there is politically very difficult.

Let me go back two steps here. The molecular analyses of animal viruses lead to the discovery of the reverse transcriptase that lead to the unravelling of the mechanism how retroviruses or congenic viruses replicate. That in turn took you to gene therapy, HIV, to the oncogenes and so forth and so on. You have covered very broad areas during your 40 year’s career. Could you tell me … In retrospect everything looks very logical, you go from A to B to C, could you tell how your science evolved, was it a logic rational approach to new problems or does it only look like that from retrospect?

David Baltimore: There was certainly never any logic in prospect. That is, I never said to myself in 1960 that if I start working on animals viruses I can go to cancer and that I can go to the immune system and development. It was little steps. I started working on picornaviruses and then I saw a little opportunity and I moved into other kinds of viruses and found the reverse transcriptase and that lead me to think about cancer and so I started some systems based in cancer viruses. Then one of those turned out to transform B lymphocytes so that was an attractive notion to go into immunology. And then, as I described to you, I also had other reasons to think immunology was interesting, so it was as if lightening had struck twice and was telling me something. I worked on Abelson virus and Abelson virus turned out to transform the B lymphocytes and I was interested in /- – -/ transfer which turned out to be a key determinant of gene arrangement, somatic mutation in lymphocytes. It sounded like I ought to work more seriously in that area so I moved into that area, did more work in that area. So, there was always a reason and always a connection between the past and the future but I was never consciously directing myself so that I would end up somewhere. I was just following my nose and then not being afraid to take a step to the side or a step in a new direction when that opportunity seemed to be ripe.

And this was showed that basic science is unpredictable, you never know where you actually go.

David Baltimore: Careers are unpredictable, at least productive careers are unpredictable. It’s not so much that basic science is unpredictable, although it is, it certainly is, and you never do know where the exciting things are going to come from. But then you have to be sensitive to them and willing to respond to them and I think a lot of people aren’t, spend their life mining just that area that they started out in without branching out into other areas and it’s a shame.

We live in a very exciting time in science today with genome projects, we have gone from viruses to bacteria to simple organism, now we have the human genome to attend to. Could you predict what this will mean for the scientific development and the implications of the human genome?

David Baltimore: There are two implications of the human genome that I find very powerful. One of them is that we have come to closure on the question of what genes there are in humans, or in mice or in other animals for that matter, plants even. Closure means that now when I do an experiment, I never have to say maybe there’s something out there I don’t know about which is causing that effect. Maybe I don’t know what’s causing the effect, but I know where to find it, it’s in that catalogue. I may not know how to read the catalogue, I mean don’t know where to look, but I know what my problem is, my problem is where in that catalogue is it all coming from, not is there something out there I’ve never seen before, nobody’s ever seen before. That’s a different way to do science. It’s a closed system rather than an open system. The other big thing and that’s really affecting how I’m doing work today is that we can scan the whole genome for its response to a given situation, just take as an example, I infect a cell with a virus. Up until now, I looked at the cell and said what was different about it by looking at specific proteins or specific cytology or specific something or other, because that’s what I was interested in, but I was never able to say what are all the changes in this cell that are going on.

Today, at least at the level of gene expression, I can say what are all the things that are going on and measure them all and that’s what these gene chips do for you, the ability to scan the genome. Again, it’s a different kind of science. At a certain stage it’s not even hypothesis driven, it’s just let’s have a look, but then all sorts of hypotheses come out of that so it’s just observational science for a moment like back in the days when Harvey first opened the body and looked inside that lead to lots of hypotheses. And that’s incredibly exciting and just nails you to do things, so having closure and having the ability to scan the whole system all at once are two things that are just going to make science different.

Thank you. We could go on for hours and days maybe.

David Baltimore: These are all the things I think about.

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