Night Science
Where do ideas come from? In each episode, scientists Itai Yanai and Martin Lercher explore science's creative side with a leading colleague. New episodes come out every second Monday.
Night Science
64 | Robert Weinberg and the perils of being a Fachidiot
MIT's Bob Weinberg is perhaps the world's most prominent cancer researcher. In this episode, Bob emphasizes that true innovation often comes from blending ideas from different fields – a synthesis that transcends the boundaries of one's primary area of research. We discuss the vital role of human interaction, with many scientific breakthroughs coming from informal collaborations between researchers, celebrating the collective "lab brain" as a powerful driver of creativity and discovery. And given that modern experimental methods could facilitate an essentially infinite variety of alternative projects, Bob recommends that we continually question the relevance of what we have chosen to work on.
This episode was supported by Research Theory (researchtheory.org). For more information about Night Science, visit https://www.biomedcentral.com/collections/night-science .
Bob
If one focuses only in what is known in one's own field, then there are many people who know that and likely derived experiments have already been done. What becomes innovative and novel is if one imports from a different area out of left field, as we say in the States, an idea that people in the field had not thought about significantly previously. Because that has the potential of generating something truly novel, and in many senses of a word, interesting.
Martin
So you're saying it's essentially because it's more likely to be original.
Bob
Well, it's more likely to be perceived as original. Yeah.
Martin
Welcome to the Night Science Podcast,
Itai
where we explore the untold story of the scientific creative process.
Martin
We are your hosts. I'm Itai Yanai and I am Martin Lercher.
Itai
Bob Weinberg is a cancer biologist at MIT, where he has worked for 60 years, since arriving as an undergraduate in 1960 though there were periods in between where he spent in other places, Bob today is possibly the world's most prominent cancer researcher, and this is thanks to the many discoveries that his lab has made, and in particular, also to the conceptual paradigms that he's put forth on how we think about what is cancer.
Martin
Bob has received numerous awards for these contributions, too many to list, but we should mention that in 2013 Bob was awarded the Breakthrough Prize in Life Sciences for his work, and his achievements include, of course, his seminal work on the Hallmarks of Cancer, which has inspired a whole generation of scientists. So we are incredibly happy to have the opportunity to talk with you today. Welcome Bob.
Bob
Thank you, Martin, and thank you. Itai, all of these accolades reminds me of an old joke about a very small and poor Jewish community in rural Poland, and one Sabbath, they were successful in recruiting a very famous rabbi to come and address them via a sermon. And so when they introduced the rabbi to the assembled congregation, they gave a very elaborate introduction. And then the head of the congregation who gave this introduction sat down next to the rabbi, and the notice that the visiting rabbi was visibly upset, and he said, “Rabbi, Have I done anything wrong? Did I miss anything?” And the rabbi said, “Well, you told them much of what I've accomplished, to be sure, but you forgot to tell them how modest I am”.
Itai
Our apologies.
Martin
Yeah for not mentioning how modest you are Bob.
Itai
So Bob, to get started, we were wondering if you could tell us overall and in general, when you think about how projects unfold in your lab, can you distill a kind of process? Is there a method to it?
Bob
Well, to begin to the extent, experiments are undertaken in my lab, more often than not, they are undertaken opportunistically in response to recent other findings in my lab, or to recent work of others, that being said, there has to be something that happens beforehand, which is to develop a taste for what kind of work and what kind of research is actually interesting and important, and what kind of research, although it yields great amounts of data, really addresses only relatively minor, trivial questions that ultimately are of concern to only a very small number of people. And in my experience, I have found that what is most challenging in training young people is to develop in them a taste for what problems are interesting and important and what problems ultimately will not stand the test of time in terms of their holding the interest of future generations of researchers.
Martin
Yeah, you were talking about a taste for what kind of work is interesting, but then you also talked about work that yields a lot of data. So, would you say that's another thing to consider that ideally it should lead to a lot of data? Or do you think a lot of data is not really what you should be looking for?
Bob
The latter, I encourage people in my laboratory to actually come up with their own research plan, as a challenge to helping to develop their own critical faculties. And sometimes people will come to me and say, Look, why don't I do this experiment? I can come up with a lot of data. And I ask them, well, having obtained all that data, what are the take home lessons that you can talk about after this work is done? Because ultimately, I demand of them that they produce a scientific opus that can be summarized in a relatively small number of sentences as take home lessons and if they can't articulate what the scope for take home lessons are, then that strongly undermines, in my mind, their credibility in terms of being able to discern what is important and what is simply adding to the compendium of publications.
Itai
And also, when you spoke about how projects get selected, you talked about moving in an opportunistic way, which is interesting, because I think in our society, that word is used as a pejorative, and yet you see it as a good thing. It's part of your process.
Bob
Well, indeed, to my mind, one needs to be able to respond quickly to findings, not only in one's own laboratory, but in the laboratories of other people. This highlights one of the bizarre aspects of the way grant funds are issued by the NIH because the National Institutes of Health requires, demands before they give granting funds that a applicant provide a detailed description of the experiments that he or she proposes to do under the support of that grant. By the time one has the grant reviewed and one actually gets funding, and if one were to strictly follow what one proposed to do six months, nine months, 12 months later, if one followed those proposals, one would be working in an anachronistic fashion, in the sense that one would be working on problems which by then had been partially solved and one will not have continually revised and updated his or her experimental agenda, which is a great because one wants to be continually revising and updating one's research priorities.
Martin
So the funding system is the antithesis to the necessity to respond quickly to new findings.
Bob
That's correct. To the credit of the NIH, when they actually evaluate one's performance, they do not hold one to have closely adhered to what one proposed to do.
Itai
That's true. Every year we have to fill out this progress report, and every year it happens to me that I look at what I said I would do, and I have to say how much I've done and every year, saying, “I said I would do that!?”
Bob
Yes, and in fact, I don't even go that far. I simply describe the progress in my laboratory on the general problem. Exactly, because I believe that NIH awards people who've been creative and who have made breakthroughs, major or minor, much more than they do review or recognize and award people who adhered closely to what they propose to do.
Itai
So, science is less like an army and more like an…
Martin
artist colony.
Bob
More like a ragtag band of independent thinking people who are not necessarily coordinated and regimented by a certain leader or by one way of thinking.
Martin
You know, we had some people on the podcast who were explaining that they like to work on problems that fascinate them and that maybe nobody else ever worked on that problem. And in that setting, I think being opportunistic makes no sense, right? Because you just have to follow your own interest, and there's no new findings that you need to respond to quickly.
Bob
Well, there may be technical advances made by others, but basically one has to be monomaniacal in focusing on this particular research project. I often cite here the career of Arthur Kornberg, who spent his entire career, much heralded, on how the innate polymerase worked, and one can applaud him for his loyalty to that particular problem, but to my mind, that's, in many senses, a rather uninteresting scientific career where he has not moved into other directions and responded to other urgent questions in biology, but instead been very self-indulgent in focusing on what interests him rather than what is intrinsically and obviously an important and interesting scientific set of problems.
Martin
So, you see yourself much more anchored in the society of science responding to what's happening and what people find interesting.
Bob
In a sense, yes, I'm not necessarily enthralled by the latest scientific finding of others, but I feel it's very important to talk with people on what problems they're working on and what they've heard recently and how they're thinking. Indeed, it may sound strange, but I wrote three editions of a cancer biology textbook, not by reading 1000s of papers, but instead by talking with people and meeting. So, each of us processes external information in a different way. That's the way I internalize and process scientific information. And try to think of what the implications are of what I've just heard, right?
Itai
And it's so fascinating to learn that you wrote this legendary textbook, and every single person working in cancer has started with that textbook. So, thank you for that one.
Bob
I feel like the visiting rabbi.
Itai
Yeah, and you're also so modest.
Itai
But to learn that that was done not from an encyclopedic study, but rather through attending conferences, just highlights how in this day of so much virtualness, there's still this importance of talking. I assume you mean face to face talking. What's your opinion of virtual conferences? Are they a good substitute? Better than nothing?
Bob
They're better than nothing. To be sure, it's wonderful not to have to jump on an airplane and waste a lot of time traveling somewhere. On the other hand, what one really loses is to confront face to face, some of one's colleagues, either singly or in groups, and listen to what's interesting them and what's troubling them, and what they prioritize as an interesting problem.
Itai
There's something that Zoom has not been able to replicate, which is when you're sitting in an auditorium and a person is presenting an idea. There's this feeling around the room that you look around, you see how other people are responding, and there's this consensus. And just a look here, a look there, so much of it is, of course, missing with Zoom, and yet it's so important for how we conclude what is this exactly?
Bob
Yeah, what captivates people and what do they find, ultimately, very trivial and boring and redundant with what they already know, right?
Martin
Yeah, so from what you just said, it's obvious that in your process, talking appears to be more important than reading.
Bob
Correct, that's my mind, and I don't say everybody should have a similarly functioning mind. I'm just talking about my own personal, conceptual, cognitive idiosyncrasies.
Martin
No, of course, of course, everybody has their own process. What I'm wondering is, is talking also central to your creative process? You know, when you're faced with a scientific problem, you're trying to figure something out.
Bob
I often come up with actually pretty good ideas. I say immodestly, when I'm talking through a problem with one of my students or postdocs, as we reason through the problem, I might think of an interesting control experiment or an interesting new direction, literally during the course of that conversation.
Martin
Can you tell us more about how such a conversation typically unfolds.
Bob
Well, one thing I like to do is to train people in my laboratory to function independently, and so when they come into my laboratory, they might propose a series of experiments, and I will respond to those proposals either by saying that's very interesting and provocative, but experimentally it's impossible, or that's a reasonably interesting problem, but ultimately, the results of it are going to be seen as being very trivial and incremental improvements on what one already knows. And then they might propose something that's actually quite innovative. And I encourage them to run with that for a while and see how that works. Run on their own for three months to six months, and we will then assess whether their chosen path has much future for them.
Itai
in these communications. Do you see them mature from graduate student in their first year to graduation?
Bob
Many mature others develop into what one calls Fachidiot in German, and that is someone who's an expert in a very narrow area. And if you ask what's going on to the left or to the right of their chosen field of research, they stare at you, they mumble and they walk quietly off because they don't have a good idea of the world around them.
Itai
Yeah, in Hebrew, we call that Rosh Katan, “To have a small head”. So that's interesting, because someone could argue that. Well, you know, for some breakthroughs, maybe the Arthur Kornberg style breakthroughs, it actually helps you to have a small head and not be distracted by other problems.
Bob
It might. But I will also add to this that, for example, for the last almost 50 years, I've been organizing a weekly meeting at MIT with participation from six to eight other groups to which attendance of my lab members is mandatory because it teaches them and exposes them to a variety of other areas of research, outside of cancer research, including mouse genetics and RNA processing and signal transduction biochemistry. I want them to be continually pelted by new areas of research about which they were relatively ignorant previously. I want them to have a rich mixture of things with the hope that some. Of these things they hear will actually prove to be useful for their own work. Indeed, I would mention that to my mind, many of the so-called creative moments in their minds and occasionally in mind, come from taking something outside our own immediate area of research and transferring it into what we do, that blending, that synthesis is often leading to things that are truly innovative.
Martin
Why do you think that is that that often ideas from other fields or things that you hear in talks unrelated to your own work give you an inspiration for a breakthrough in your own field?
Bob
Well, if one focuses only what is known in one's own field, then there are many people who know that, and likely derived experiments have already been done. What becomes innovative and novel is if one imports from a different area out of left field, as we say in the States, an idea that people in the field had not thought about significantly previously, because that has the potential of generating something truly novel, and in many senses of the word, interesting.
Martin
So you're saying it's essentially because it's more likely to be original.
Bob
Well, it's more likely to be perceived as original. Yeah, different area of research, really, what's original about it is fusing two different areas of knowledge into one, or combining them in a way that had never been combined before. It's the combinatorial interactions between work of others in another field of research and work in one's own subfield, which, to my mind, yields novel and even interesting outcomes.
Itai
You know, that brings us to the overall overarching theme of this podcast, which is night science. You know, in his autobiography, “The Statue Within”, Jacob portrayed the process as he experienced it, which was not linear, and you're not in this realm of hypothesis testing that he called day science. Rather, you're in the realm of hypothesis generating or just being confused. So, he called that part night science. And I guess I'm wondering if that resonates with how you experience science, that there's these two realms, the part where, okay, let's talk about the controls of this experiment, but then this other world, where we think about ideas?
Bob
Well, I'll give one anecdote, in the mid-1970s one had essentially three different competing theories of how cancer cells arose. One of them, which had relatively little. if any experimental support, was that cancer cells are actually genetically different. They are mutant cells. In retrospect, it seems now obvious that that was the case, but that was only one of several alternative hypotheses. Somehow, people said X rays cause cancer, or chemicals cause cancer, or viral infections cause cancer. And one deduction from the genetic hypothesis was, as I just mentioned, that cancer cells have mutant genes, and indeed, those mutant genes are responsible for the aberrant behavior of the cancer cells that carry those genes. And in 1978 I was walking across the Longfellow bridge in Boston, connecting Cambridge to Beacon Hill, Boston. And was puzzling about this problem, having to trudge through three feet of freshly fallen snow. And while I was doing that, I was thinking about experiments that had taken place in my lab, in which one could take DNA from cells that had been transformed by a sarcoma virus infection and introduce that DNA into the genomes, into the cells of untransformed, non-neoplastic cells. And on occasion, one could actually observe the transformation of the cells that had taken up the donor DNA, and in fact, that experiment worked and led me to a simple and incrementally improvement on the conclusion, which was that one might indeed be able to detect the presence of a cancer gene in cells that had never experienced Aaviral infection, but instead such cells having experienced transformation through the actions of a mutagenic carcinogen, and that was the idea I came across, and the realization that we were now experimentally capable of actually testing that hypothesis, and so that energized me enormously. I thought this was a really original and great idea, and so I coerced one recently arrived graduate student to start working on it. It being experimentally very challenging, and being very excited and proud of my newfound originality, I discovered that actually three months. Was before my trudge across the Longfellow bridge, I had read about and heard about work of another researcher in Canada who had demonstrated that DNA from cancer cells can actually transform normal cells into which it had been introduced. And so, I came to realize that my one original idea was actually probably inspired by a result that I had come across and then tucked into the back of my brain, far away from my conscious thinking.
Itai
Although this other lab was corrupt in some way, right? They cheated.
Bob
In fact, the earlier experiments, while conceptually interesting, had never occurred at all. They were all, as we say in the business, dry lab. They were concocted.
Itai
Oh, when you say dry lab, you mean something that was not actually done.
Bob
Exactly, right. Never involved getting one's hands wet at the laboratory bench. And we needn't go into that scandal. The take home lesson was that my idea was not original at all, but in fact, the evidence that was initially adduced to that problem turned out to be fake. That didn't deter me, because I continued to think this was an interesting idea and worth pursuing in great depth, which yielded what was ultimately the most important finding in my career, we have to recognize that the fact that the initial idea was, in fact, concocted without any underlying experimental proof turned out to be irrelevant.
Martin
I guess the original idea was valid, right? It's just that they didn't bother with the experiment.
Bob
Absolutely
Itai
it was so valid, why test it?
Bob
In jest, do people my laboratory again, in jest I say, don't bother me with the experimental results. What's the idea? Realize I'm speaking ironically.
Itai
Yeah,I thought you would say, don't bother me with the results. I've already made up my mind.
Bob
Well,that's what I'm saying. That is obviously outrageous, that it sparks a reaction, an unconscious one in the minds of those who work in my lab, a reaction that in fact, these results are indeed critically important to sustaining and supporting an idea and simply building castles of ideas. One concept-based plot piled on another is nothing more than a house of cards.
Martin
Yeah, that's the power of science compared to philosophy. It's not coming up with ideas. Philosophers are great with that. It's about throwing out the bad ideas through experimentation, through data.
Bob
That raises the question of how many ideas there are in biology, and the fact of the matter is, the number of experiments one can do in biology currently, given the power of existing technologies, is vastly more than the number of stars in the universe. I'm continually imprinting on the thinking of people in my lab or my trainees, that there's so many different things they can do. Why do they focus on this one? How arbitrary is it? And how can they defend utility and the importance of what they happen to be working on?
Martin
Isn't that scary? When you tell them that?
Bob
It's supposed to be scary, it's intentionally scary. It provokes them, hopefully, into a defensive posture where they find and defend and justify what they're working on. And if they can't do that effectively, that should be and is very troubling to them,
Martin
Yeah. And as you say, it shouldn't be troubling to them, yes.
Bob
So, that's one might call that productive anxiety.
Itai
We take a quick break from our discussion to thank our sponsor. Night Science is supported in part by Research Theory, a nonprofit working to improve creativity and culture and science. Find out more at researchtheory.org
Martin
Questions that r Research Theory asks, for example, are, where do ideas come from? What work will be remembered in 100 years? Can you measure creativity? Is creativity static or dynamic? We are very grateful for them asking such questions and for their support.
Martin
So you've been talking about the necessity to develop a taste for what kind of works interesting, right? What is the criterion? Can you describe it? How can you recognize something as being interesting?
Bob
Well, of course, one can paraphrase what the Supreme Court once said,
Itai
You know it when you see it.
Bob
I know pornography when I see it. The fact is that what one has to do unconsciously with every passing month and year. Refer back to what are the big problems that are hobbling forward progress in the field? What are they at present? And unless one asks that without the pretense of answering or addressing all those problems, then ultimately one can drift into obscure lines of research which are of no interest to anyone. Now you may think, doesn't that mean pandering to the crowd? And in fact, one has to think, why are they of interest? Why do many people embrace an understanding of these problems? Or why are they ultimately no more than stamp collecting? Collecting mindless phenomenological data, which yields almost no insight into biological function.
Itai
Well, I know what you mean about stamp collecting. It's just that you could have a lot of surprises that arise. Sometimes you just don't know ahead of time what the surprise will be, because it's a surprise. And so I think there's got to be some balance where, of course, you can't document every rock in the trail that you're on, but you should document some things, right? You should allow for surprises in that way.
Bob
It's absolutely true. But the fact is, you shouldn't depend on the inevitability of surprises. If you're working on a problem and you're counting entirely on that problem yielding surprises, you may be moving into a swamp where that problem may never yield surprises. Whereas, if you're working in an area that has, for one reason or another, been thought to be important conceptually and biologically, then you're more guaranteed to find something interesting, maybe not surprising, but interesting by many criteria.
Martin
Yeah, Itai, I'm actually guessing that you're defending this type of work, because that's essentially what you do. You like to say,” Okay, I'm interested in this type of problem, and if I now create data which combines this aspect with that aspect. I'm sure I'm going to find out something interesting about that type of problem”, right?
Itai
Exactly. I think I look at it as, what would call it, like a jigsaw puzzle that at the beginning you're just trying to say, what are the pieces that I'm working with, what's sort of possible, and it's through that mapping of the landscape that maybe new ideas could come about, which will then be subjected to rigorous testing, but at least that's where the hypotheses could come from.
Martin
Yeah, but I think that's really exactly what Bob was describing, right? Like, even if there was no surprise, you would still have a new jigsaw puzzle that would reveal some details that were not visible before. It's just that you're hoping that on top of that, you might find a discovery.
Bob
One can find all kinds of surprises, for example, in the area of evolutionary biology and the six to 10 million species of metazoa that exist on the planet, one can find very interesting and unanticipated evolutionary adaptations. Those adaptations are idiosyncratic, and no one could have predicted them a priori, given the vagaries of evolution and the fact that ultimately, we complex organisms are the results of Rube Goldberg inventions, contraptions that are cobbled together in different ways to somehow yield function. And so, one has to ask the question, let's say you come up with an interesting and unanticipated way by which Protochordates developed a defense mechanism of one sort or another, is that the fact that they'd come up with a solution, which is somehow surprising, worth your three years of life in demonstrating that it existed.
Itai
I guess one thing I worry about is that in developing taste, are we necessarily becoming better scientists, or are we also giving away something maybe becoming too Arthur Kornberg over differentiating,
Bob
Well, one has to give away something, because as one grows older, one's universe of possibilities grows narrower and narrower. When I was 15, I thought about many different things that I might be doing, but as I grew older and older, I became to realize that there's lots of things I could never conceivably do, and so I had to narrow my ambitions and my interests. I long ago concluded I would never be able to learn Chinese, and so that was a narrowing experience. I would never become an Olympic skier, not that I aspire to any of these things, but they led me to confront the reality of one's mortal existence and the fact that the older you get, the more narrow one's possibilities become. And as you just mentioned, Itai, the narrower are one's intellectual horizons. One begins to focus more and more, because a lack of such focus just ends up being a dissipating of energy, intellectual and financial energies.
Itai
So do you think there are scientific problems? If you think about it strategically, these are the ones you should work on now, Given how your career has evolved, you maybe couldn't have conceived of doing this earlier, but maybe it's big enough, broad enough, that you could take this on now.
Bob
Well, one problem I've wrestled with at a distance is the following. You know that when signals come into the cell, there's a very complex signal processing circuit in the cytoplasm of the cell that processes this incoming information and ultimately makes a decision as to whether or not a cell should divide or not, whether or not a cell should survive or not, whether or not a cell should acquire a whole new series of differentiation phenotypes or not. And the circuit is extraordinarily complex, well beyond our current intuitive ways of accessing any understanding. And the question is now whether someone with the much-touted skills of artificial intelligence could begin to understand how this circuit operates. You come to realize that at present, this is vastly beyond our ability to understand how the circuit actually operates, and so one now has the tantalizing possibility that AI will throw us a lifeline. That's what I consider now that I could never have conceived of considering decades ago,
Martin
interesting. I'm totally fascinated by the influence that AI has started to have and will have in the future on science and possibly also creativity. I would be curious about your opinion on that. Do you think that AI currently is useful or will be useful also for the creative scientific process?
Bob
Well, I don't claim to be an expert on AI. On the contrary, I'm just viewing it at a great distance with no expertise whatsoever. And I'm just stunned by the success that AI has had in predicting the three-dimensional structure of proteins, a problem which many have wrestled with over a period of half a century. And I can only extrapolate from that the fact that AI will one day be quite successful and predicting the combinatorial actions of multiple independent agents or multiple independent parameters. And so, looking ahead in five or 10 years, I can imagine that AI will be of enormous utility in trying to understand how complex signaling circuits operate. So, this is a bit of a speculation on my part. It may or may not happen, but as the famous baseball catcher, Yogi Berra once said, “The problem of predicting the future is that it hasn't happened yet”.
Martin
Yeah, he was great.
Itai
You know, it reminds me what he said that pertains to our previous discussion, that you can see a lot by just looking.
Bob
By the way Itai, this raises the question of whether gathering very complex data sets will inescapably yield interesting insights. And I mentioned many examples of situations where one has accumulated extraordinarily complex datasets that have just been archived in many 1000s of feet of research journals without their ever yielding any interesting insight. And so accumulating large data sets is on its own, something which still requires much justification. Of course, those who do that will say, just wait. You'll see what our data will yield. And I'm unconvinced that everything they're doing and all the data they're accumulating will one day culminate in the coalescence of multiple alternative ideas and novel conceptual insights. Because conceptual insights, to state the obvious is what I am focused on, monomaniacally,
Martin
I guess if you're going to collect a lot of data, at least you should have some idea of how it's going to give you insights.
Bob
You should have at least a pretense of hoping that it will yield insights.
Martin
Yes, yes. So, that should console Itai. So, Bob, we've talked a lot about different aspects of your process. Is there something that you feel we haven't spent enough time talking about as regards your creative scientific process?
Bob
Well, I think an important aspect of the creative scientific process, it's the human interactions one has with those who one works with one often dismisses as peripheral and irrelevant. The nonscientific interactions one has with people and one's ability to act in a synergistic fashion with them, to collaborate, to create things which each individual in a collaboration would not have created or thought of on one's own. So, there's much about, let's say, the inner communications between people in a research group which are not really well understood and to my mind, represent strikingly important elements of understanding how scientific progress is made in my own group. Often, somebody will come up with an idea that came from their having read a journal article, and it's something that never would have occurred to me. And in fact, I say in utter honesty and frankness, many of the best ideas in my research have not come from my own brain, but rather from the brains of my trainees, of postdocs and graduate students. They're the ones that often introduce new and novel ways of thinking, and that, by the way, is what's critical to running a scientific enterprise, having a group that has a critical mass, that has enough people that can constantly and continually be feeding each other with interesting ideas that a single individual, on his own or her own would not have anticipated.
Itai
Bob with this statement, you really earned the title of being modest to say that others have come up with the ideas. I would say that it's not maybe just you, or maybe not just them, but the lab's brain. You know, it's like a synergistic interaction, the collective. And if you wanted to really punish a scientist, you would probably do the same thing that happens in jails, unfortunately, is you put someone into solitary confinement. That would be just as bad for a scientist, right? Imagine if you couldn't talk to another scientist. So, I absolutely agree that so much comes from these interactions,
Bob
And by that way, raises the question of critical mass. How large do you need to build a scientific group in order for it to be truly functional and innovative? To my mind, scientific groups that are too small ultimately and rapidly become too narrow in view of the world, in their well-done job.
Martin
But doesn't that depend strongly on the topic that you're working on? If you're working on something very general, like cancer, right? Like where there's so many different directions in which people could go. And so many groups working on it, I can see the critical mass thing. But if you're working on something much more specific, do you think it's equally important?
Bob
Well, I cannot speak to things much more specific. I can only mention the fact that in my research group, when someone comes up with an idea for research, I ask them whether it's interesting, whether it's doable, and how it relates to the research skills that exist in my lab. In other words, if somebody were to come into my lab wishing to undertake neurobiological work, I would say, “Well, that's very interesting, but it's not within our area of expertise. Why do you want to be in my group?” And therefore, relates to the question of how one defines the boundaries of one's own areas of scientific interest. Are they infinitely far apart, or can one actually define them, with some precision, as being areas where one hopes to be able to be productive? How does one draw those boundaries, and how rigidly does one impose them?
Itai
You also said, Bob, that maybe too small of a group is inhibiting. How big do you think is too big for a lab?
Bob
In my experience, labs with more than 10 or 12 postdocs, for example, some of them may be very productive, but if you examine carefully the bang for the buck, how much do they actually do in terms of innovation compared with the enormous amount of resources that they use or that they squander, then one could begin to imagine that if you have groups that are much larger, not only are they less useful economically in terms of producing new insights per dollar, but also, and even more importantly, they no longer yield good training to the individual postdocs or students. In other words, I know people who have groups of 20 or 30 researchers in them, postdocs and students and even undergraduates. And one can ask oneself, given that size, how much training do the individuals in that group actually receive?
Itai
Someone should do a sociological study on what is the ideal range, and then the NIH should enforce it, perhaps.
Bob
Well, that would be a little bit too draconian. An ideal size depends on the capabilities, among other things, of the leader, how flexible and adaptable and far reaching is his or her intellect, and how many people can they actually effectively deal with. They may be capable of obtaining large amounts of grant funds, many, many millions of dollars as a testimonial to their grant writing ability, but that may not be mirrored by a compensating ability to effectively train all the people in their labs. Of course, this raises the whole other question of how often is research or should research be intimately coupled with training. In our world, in our society, we do come. All the two things, but maybe it's good just in certain cases, to have an army of technicians to just crank out different kinds of results. You can ask the question, for example, in those that cranked out the human genome sequence in the early years of this millennium, how effective, how productive were many of the authors of that work in terms of their subsequent scientific careers, or did they actually become what I mentioned before, Fachidiot, experts in the narrow area of technical advance, masters of one very narrow area, but ignorant of all other areas.
Itai
Yeah. Yeah. I mean, I think in general, each project could be narrow, but the projectee, the person doing the project, needs to be broad. Yes, yeah,
Martin
Bob, that was a really interesting discussion we had. I learned a lot, and it seems that you have your very personal style of how you think about research and how you think about defining research problems, I found that really fascinating.
Bob
Well, other people have totally different ways of looking at science, and I would not disparage those alternative ways. I'm just an owner of a very idiosyncratic personality and brain.
Itai
And also very modest.
Martin
No, but what I wanted to add is - yes, of course, different people have different styles, and we need those combinations, and that's one of the purposes of why we do this podcast, right? So, that the listeners can get an idea of all the different varieties that are out there and that are each by themselves, incredibly successful.
Bob
Potentially, incredibly successful. Some yes, some no. But if one does not have diversity in terms of one's style, then one is doomed to a very regimented and narrow and predictable series of outcomes.
Itai
Well, thank you so much for joining us today, Bob, this was extremely interesting. Really appreciate your time.
Bob
It's my honor, my pleasure to talk with you. Well, with luck, maybe one day we will meet in one place or another.
Itai
Would be fantastic.
Bob
Well, it's less and less likely, given my age, but anything can happen.
Itai
We look forward to it.
Martin
Yeah, would be wonderful.
Itai
Thank you again.