Recorded: 22 Aug 2008
So the telephone call said they already had set up a committee, with all these Nobel Prize winners on it, some of which like Wally Gilbert and Jim Watson were saying, “It’s a no-brainer. Let’s just go and do it! It'll take 3 years.” That was Wally Gilbert’s point. “No point in studying it if we should do it!” Others like Shirley Tilghman, now President of Princeton University, or David Botstein had been arguing strongly against this. It would ruin biology. It would make biology big science and it should be small science. And I couldn’t figure out for the world why they wanted me to chair this thing. I said “I have never even thought about this. Why do you want me to chair this group of very contentious people all with strong opinions?” And they said, the answer was, I think not completely truthful because I think now I understand why I was. But the answer was ’cause we’ve never thought about you having any opinion you could be unbiased. But actually the idea of actually chairing anything with these characters on it…like Jim Watson was you know an incredible challenge. And so I decided to do it because I’m sort of a sucker to take on difficult projects all my life. Anyway, it turns out the real reason I think they wanted me was that I had published a small editorial comment in Cell in 1985 about in biology small science is good science, arguing for small labs, which I still believe in. And, therefore, if the committee that I had chaired came out in favor of the genome project then it would have more credibility with scientists, most of whom were really strongly against-most biologists were strongly against what they thought might be a perversion of our whole system of doing small science. So, at any rate I figured this out, it took me a long time to figure that out. But the committee was a fascinating experience because how you get people to come to consensus when they already start on completely opposite sides. And John Burris and I designed this strategy which turned out to be very successful. Basically we wouldn’t even discuss recommendations until we had sort of set the whole background. We had all these chapters we were going to write on the background of all these issues, like genomics and genomic mapping and sequencing and things like this. And meanwhile we would call in people, young people who were actually working on the sequencing methodologies and try to-I said try to bring truth to Washington. Because there was all these important people who had never actually testified [unintelligible] for years who were saying how easy it was. At any rate we did that at every meeting. We called on some young people on the front lines to actually learn the realities and try to educate the committee before we would let anybody even start to consider a vote on it. I knew we would never get consensus at the beginning. One of the most successful young people, most impressive, was Maynard Olson who at that time was a very young person. It ended up, we put him on the committee. Wally Gilbert ended up resigning put Maynard on the committee. He was a very important member of the committee because first of all he was very thoughtful and articulate. But second of all he actually was doing this stuff and could say why these simple schemes that many people proposed will not work. So, you know, we came up with a strategy which was immediately adopted by the government. Actually, Jim Wyngaarten who was head of the NIH really pushed us and he deserves a lot of credit. Because most of the people at NIH as usual said they were already doing this and we shouldn’t do anything different. But Jim Wyngaarden was very strong on this. And we said don’t do massive sequencing until you could get the cost down below 50 cents a base pair which was probably 10 times cheaper than it was then. And meanwhile work out the technology by sequencing what we call model organisms because there’s going to be homology between genes of yeast and fruit flies and worms and the genes of humans. And those are experimental organisms where you can actually figure out much more easily than we can in humans how genes function and what they do. And we’re going to need that information anyway, so shouldn’t…the strategy was, get that information on small genomes where it’s easier and you don’t spend a lot of money at $5 a base pair. While you get the technology to improve. If gets below 50 cents a base pair then try to do the human genome. That’s exactly what happened. But we were lucky because the homology turned out to be enormously more than we had any right to suspect. I mean, at that time we probably thought that, you know, 10 percent of the yeast genes would be relevant to humans. In fact, almost all of them are. And that whole strategy has been incredibly powerful. Another thing we had to argue against, the second thing was that the other alternative was not the sequence, but… or sequence in any event you know…The major argument of a lot of people was just let it happen. It will happen eventually and we’ll sequence the human genome. We said, no. We need some technology development. We need to have special programming. Part of that argument was that people with human material were not sharing it, and, you know, people I’d say with patient population with cells. The strongest argument that I think that brought us all together in favor of a genome project, including Botstein and Tilghman and all those who were against it, was that we need to enforce a sharing ethic. And if we had new money and a special project we could make people share. That was the only way this was going to get done efficiently. So sequence or not, sequence, we decided to sequence. But the second thing…what to sequence. Because there was a strong contingent saying, Well we should only sequence the transcribed regions, so called cDNA, ’cause that would be like 1% as much sequencing and all the rest was junk anyway. And again we argued that there was going to be some information that wasn’t expressed, and that some of that junk was going to be interesting junk. And in fact again we were incredibly lucky. We now know that there’s twice as much DNA that’s highly conserved and functional as there is DNA that’s normally get from expression clones; that is the cDNA clones. So the yield from sequencing the whole genome has been enormous.
Bruce Alberts, currently Editor-in-chief of Science, Professor Emeritus in the Department of Biochemistry and Biophysic at the University of California and United States Science Envoy. He received A.B. (1960) in Biochemical Science from Harvard College, Cambridge, Massachusetts and Ph.D. (1965) from Harvard University, Cambridge, Massachusetts. In 1966 he joined Department of Chemistry at the Princeton University and after 10 years he became professor and vice chair of the Department of Biochemistry and Biophysic at the UCSF.
Alberts work is best known for his work on the protein complexes that allow chromosomes to be replicated. He is one of the authors of The Molecular Biology of the Cell, a major textbook in the field. He served two-six years terms as a president of National Academy of Science (1993-2005). During his administration at NAS, he was involved in developing the landmark of National Science Education standards.
Among many honors and awards (16 honorary degrees), he is Co-chair of the InterAcademy Council and a trustee of Gordon and Betty Moore Fundation.
More Information: Wikipedia,