Recorded: 15 Jun 2002
My advice is too old-fashioned for this generation of scientists.
Well, I think there are a lot of problems in science today that I didn’t experience when I was a trainee and I’m aware of the differences. I think that one of the problems that people face today is that there are so many journals and so much information being published, let’s forget about what’s on-line; just talk about hard copies of papers. There are so many papers and there’s such a vast literature that I think that it’s almost impossible for any member of the scientific community as an individual to process all that information.
So even if we’re diligent in reading and, you know, I get fourteen journals at home. And even if we’re diligent in trying to go through them, there’s just no way to remember everything you’ve even looked at. And so a lot of people don’t even look.
I have a lot of colleagues who learn things at meetings—they’re walking up and down the hall of their institution or Xeroxing papers that they’ll never read. They just look at the abstract. And on this basis they assign priority for discovery, which is a problem. And they permit major errors to occur in the literature which get compounded. So I would say, a very high percent—a percent that probably much higher than people imagine—a very high percent of what’s in literature is wrong to me. That’s my view. And much higher than people would say, you know, what would you accept as a good error frequency? Five percent incorrect? A two-sigma error—P-value less than whatever, right? But it’s much higher than five percent. There are a lot of things that are in the literature that are just simply incorrect.
And my colleagues and I talk about highly cited famous scientists whose work we know is wrong. But nobody can ever seem to catch up with them because they’re always publishing the next Cell or Nature paper. And, you know, it’s almost impossible to have an accounting.
Moreover, we pressure our students and our postdocs by saying that if they don’t have papers in frontline journals, they’re not going to get a job. Whether that’s true or not, I won’t debate. It shouldn’t be true, of course. It may be true. And so this puts a lot of pressure on young people to get an exciting result. And if that exciting result involves a little bit of compromise in terms of the rigor of the experiment, my guess is that a lot of people fall victim to that kind of thinking.
And so, as the error frequency increases, of course, many people get glamorous papers, but it doesn’t mean that the science is going to take us anywhere. And as we publish more and more things on-line, and as we do less and less review work and as the number of papers published exceeds our capacity to really even comment on the quality of the work, suddenly the standards are eroded. So I try to tell my people what my standards are, but at the same time they argue with me; they think I’m probably being too rigorous and not very realistic. Although I can’t really compromise.
… I think each of us has our own private view of biology and our field of expertise. We put the story together conceptually in the way we see it as individuals and we use that, I would say, incomplete mosaic of information to try to create a picture. And so the intuitive aspect of science is that my picture may look different from yours. In other words, if you consider a mosaic, which has no picture, but there are tiles around and you imagine how you’re going to fill in those spaces by doing, in our business, an experiment rather than painting. I might do different experiments than you with the same data or the same panorama as we see it. The issue really is that you and I may see the incomplete picture very differently and we may have very different hypotheses about what we plan to do. And so the experiment that I choose may be very different from the one that my colleague chooses. And then the issue of what’s right comes from validation from other people. And exciting work unvalidated isn’t discovery. It has to be correct at the end.
… I mean I’m in a different stage of my career. I don’t mean, you know, I think people go through different phases. So, you know, there’s a phase where you have to be productive. And if I gave you my C.V., you’d see that there was a phase where I’m just publishing like a madman. One of the interesting things about my postdoctoral fellowship was that I was enormously productive. And I published an embarrassing number of papers of marginal interest, I would say in retrospect: I mean, you know, part of the archival literature that even I don’t remember. But there are a lot of papers. And when I moved out and I took an independent position at the N.I.H. in 1977, so now it was my lab; I vividly remember when Hidesaburo Hanafusa came and visited the laboratory and he sat down with me. And he had always actually been very nice with me about work and he was a good person in the field, sort of helping out, giving advice and so on. He liked me even as a young scientist. But I’ll never forget that when we sat down in my office the first thing he said—I had fifty publications—and we sat in the office and he said, “So, you’re on your own now.” I said, “Yes.” And he said, “Well, we’ll see.”
… the one’s that I had done with other people, and the fact there were a lot, a few, or whatever; they didn’t matter. Now that I was by myself his comment, “We’ll see”, means now you have to show what you can do. All the rest is just training. I thought that was an important lesson for me. I was very upset, but I thought that—you know, that I wouldn’t have to prove myself, but “We’ll see!”
So, I mean that was a good experience.
Oh, so—let me just make the point—I didn’t mean to digress, but I wanted to say that the young people in my laboratory want to be productive, they want to publish. But real discovery may be just one paper—an important paper, rather than ten that you can weigh, you know. And even ten in good journals that will be forgotten are not as good as one really killer paper, which simply changes the way people think. And without specifying what area of interest it’s in, I think that’s a general rule. And so I tell my people to try to, you know, ask a significant question. Not just waste their time writing another paper.
Now for me—thirty years out—however long it is, right, I mean, I haven’t really thought about it, but something like that. You know, thirty years away from my degree; writing another paper is no thrill. So I’m not trying to be productive. I’m just trying to see if I can still do a significant experiment. And so I tend to direct my people that way. And they say, “I need papers. I have to get something out of this.” And I say, you know, “You need to make a discovery. You need to do science. That’s what it’s all about at the end.” But in a way, I’m imposing my experience on a much younger person. It may not be entirely fair. And at the end you need to balance their needs with your own perceptions, so it’s difficult.
Charles Sherr earned his joint M.D./Ph.D. degree from New York University in 1973. He is a Howard Hughes Medical Institute (HHMI) investigator based at the St. Jude Children’s Research Hospital in Memphis, TN. His work focuses on retroviral oncogenes, growth factors and their receptors, and cell cycle control. In 1991, Sherr's laboratory discovered the mammalian D-type G1 cyclins and went on to identify the cyclin-dependent kinases with which they associate, as well as a series of polypeptide inhibitors that negatively regulate their activities.
Sherr is a member of the National Academy of Sciences, has won numerous awards and is the author of more than 235 scientific articles. He joined the National Cancer Institute in 1973, becoming a member of the NIH staff in 1975 and head of the viral pathology section, Division of Cancer Cause and Prevention, in 1977. In 1983, he relocated to St. Jude. Sherr is also a member of the Board of Trustees of Cold Spring Harbor Laboratory.