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Molecular Biology of the Cell Vol. 3, 385-388, April 1992

Ideas are Becoming an Endangered Species S.J. Singer Department of Biology, University of California at San Diego, La Jolla, California 92093

Those of us who have been active in the field of molecular cell biology for two or more decades have seen profound changes in the structure and the modus operandi of our science. One of the consequences has been a decline in the importance of ideas. It used to be that ideas were critical to inform experiments over a long term, to suggest which experiments among innumerable possibilities should be undertaken, and to provide a conceptual framework with which to think about a problem. However, this was before the advent of the powerful technologies of molecular genetics and the use of recombinant DNA, polymerase chain reaction, and monoclonal antibodies. For many research problems today, a tremendous amount of new and previously inaccessible information can be obtained without any preceding or informing ideas. By inducing mutations in suitable organisms and by the selection of appropriate phenotypes that exhibit different characteristics for the property under study, new genes with important functions can be cloned and sequenced. Examination of the protein data banks for homologues is then supposed to tell us what the protein molecules that have been thus discovered might be doing in the cell. As an alternate approach, a monoclonal antibody can be generated that shows an immunocytochemical labeling pattern suggestive of a specific function for the antigen detected. Again, cloning and sequencing of the cDNA, and the search for identities or homologies between the protein and those in the data banks, may tell us what biochemical function the newly discovered molecule may perform. After identifying such proteins, one can then do all kinds of other experiments that are conceptually straightforward: one can generate molecular chimeras, or specific deletions, or carry out site-directed mutagenesis of any number of amino acid residues to explore how these molecules work. These procedures, tossed off so glibly here, involve a lot of hard work and are very time consuming. The information they produce can often be astonishing and unexpected and immeasurably more detailed than has heretofore been possible in this field. There is no desire on my part to denigrate these efforts; on the contrary, 'Taken in part from the E.B. Wilson Award address given before The American Society for Cell Biology at its annual meeting in Boston, MA, December, 1991. © 1992 by The American Society for Cell Biology

they have been, and will for some time to come continue to be, extremely fruitful. Nevertheless, the power of these operations has apparently rendered ideas much less important, even dispensable, for our science, and this presents problems. Can molecular cell biology in the long term prosper without informing ideas? And what happens to our better young scientists who have to function in such an intellectual climate? Before discussing these problems, let me indicate what I mean by ideas in the context of this article. I am not referring to ideas about what experiments to do the next day or week. I am concerned with larger informing ideas. There are at least two kinds of such ideas. One kind addresses the questions: how does some molecular or cellular process work; what might be its molecular mechanism? The other, how can something be done experimentally, e.g., what scheme can be invented to sequence DNA, or to label antibodies to visualize them microscopically, or to select rare phenotypes among a battery of mutants? The pursuit of the second kind of ideas is flourishing and does not need any encouragement to continue to prosper. It is the first kind that I refer to as an endangered species. It might be useful at this point to give an example of such an idea about how things might work. For this purpose, I bring up an idea put forward by Linus Pauling. To appreciate it, however, one must transport oneself back to a prehistoric era in molecular biology, back to 1948. At that time, the genetic material was not yet widely accepted as DNA, and the elucidation of the double helical structure of DNA was 5 years off. Many thought the genetic material was protein in nature, because it was considered that only protein was sufficiently variegated to serve the purpose. In any event, a key conceptual question was, how could a macromolecule be duplicated to yield a very large number of identical copies of itself? If one can adopt a clean mental state, a tabula rasa, that predates the DNA double helix, one will appreciate that this is a formidable conceptual problem. In 1948, Pauling suggested the following idea (Pauling, 1986): "If the structure that serves as.... the gene. . . . consists of, say, two parts, which are themselves complementary in structure, then each of these parts can serve as the mold for the production of the replica of the other part, and the complex of the 385

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two complementary parts thus can serve as the mold for the production of duplicates of itself." There are many things that can be said about ideas, but I mention only three. First, as the quote just given illustrates, ideas can be breathtaking, particularly in retrospect. They are nothing less than the poetry of science. Second, ideas do not come out of nowhere. They arise in an individual mind from associations made with other ideas or information that is stored in that mind. In the case cited above, it seems likely that Pauling's earlier ideas about an instructive theory of antibody formation (Pauling, 1940), in which an antibody molecule acquired its specific binding capacity by folding about the antigenic determinant acting as a mold or a template, played a critical role in his scheme for complementary templates in molecular reproduction. The third thing I want to say about ideas is that one has to have the courage of one's convictions about them. This can be extraordinarily difficult and demanding, perhaps much more so than the generation of the idea itself. It is one thing to have an idea, but it is quite another to be confident that it is the unique and correct explanation of a phenomenon and to commit oneself to act on that conviction. This becomes especially intimidating if the idea is truly original because-almost by definition-most colleagues will think that it is insignificant or wrong. It is difficult to imagine Pauling ever lacking the courage of his convictions, but when he and Corey came some years later to propose a triple helical model for DNA (Pauling and Corey, 1953), that model did not reflect the twofold complementary structure that he had originally conceptualized for the genetic macromolecule and that was indeed the critical feature of the correct solution. To descend from the stratosphere back to earth, I have been fortunate enough to have generated some ideas about the molecular organization of membranes and about the molecular basis of membrane functions (Lenard and Singer, 1966; Singer, 1971; Singer and Nicolson, 1972). Some of these ideas are listed in Table 1 and have been discussed in a recent review (Singer, 1990). I consider here only a few of these ideas. Again, one has to go back to an earlier time, in the 1960s, when the Davson-Danielli-Robertson model of membrane structure was widely accepted. In this model, the protein molecules of the membrane are unfolded polypeptide chains sandwiching a lipid bilayer. This seemed to me to violate thermodynamic precepts about protein structure (Kauzmann, 1959) that had become prevalent by the 1960s, and so John Lenard and I suggested instead that membrane proteins were characterized by amphipathic structures (Lenard and Singer, 1966) with hydrophobic domains embedded in the bilayer and hydrophilic domains protruding into the aqueous phase. At this time no membrane proteins had as yet been characterized structurally. 386

Table 1. Some predictions about membrane proteins a few years B.C.' 1. Existence, structures, and functional characteristics of integral and peripheral proteins 2. Amphipathic structures of integral proteins a) Large free energy costs to bury ionic amino acid residues (and saccharide residues) in nonpolar environment b) Possibility of transmembrane proteins, with two exposed hydrophilic domains connected by hydrophobic buried domain c) Impossibility of entirely buried integral proteins 3. a-Helicity in transmembrane domains a) Free energy loss if interpeptide H-bonds are not efficiently made in the membrane interior b) Because the a-helix is the most efficient way to form the maximum number of interpeptide H-bonds, hydrophobic domains should be extensively a-helical 4. Existence of transmembrane channels a) Transmembrane subunit aggregates can form a central waterfilled channel across a membrane b) Ionic residues can be present within the water-filled channel c) A quatemary rearrangement of the subunits, requiring only a small free energy input, powers the translocation of ions and small hydrophilic molecules through the channel a

B.C., Before Cloning.

Where did these ideas come from? They arose by associations derived from a quite different area of study. During the 1950s while I was in the Department of Chemistry at Yale University and functioned as a physical biochemist, my colleagues and I carried out a number of structural studies of proteins dissolved in nonaqueous solvents. These studies were subsequently collected in a review (Singer, 1962). Our results along with those of others showed that the conformations of protein molecules strongly depended on the nature of the solvent. In particular, I stated in the review that "the cellular environment of many proteins contains high concentrations of lipid components.. . . in a wide variety of cellular membranes. The gross conformations of these proteins in situ might be determined by this association with a nonaqueous environment." This mental association provided the basis for the eventual development of the fluid mosaic model of membrane structure. It seemed clear to me at the time that the amphipathic structure of membrane protein molecules would render such proteins insoluble in ordinary aqueous media because their hydrophobic domains would keep the proteins out of solution. It was therefore a disturbing fact that some membrane-associated proteins were readily soluble in aqueous solutions; for example, it was well known that cytochrome c of mitochondrial membranes could be solubilized by treatment with 3 M KCl. Furthermore, the ready solubility of such proteins made them particularly amenable to study, and they were being represented by some investigators as paradigms Molecular Biology of the Cell

Ideas: An Endangered Species

of all membrane-associated proteins. In retrospect, I realize that at this stage I did exhibit the courage of my convictions. To account for what I considered to be discrepancies with my model, I proposed that there had to be two kinds of membrane-associated proteins, integral proteins that had amphipathic molecular structures, and peripheral proteins, like cytochrome c, that resembled ordinary water-soluble proteins (Singer, 1971; Singer, 1974). I suggested that the peripheral proteins were attached to the membrane by specifically binding to the hydrophilic domains of certain integral proteins where these domains extended into the water phase. This could account for their specific association with, as well as their relatively easy release from, the membrane. This idea is commonplace today and is the basis, for example, for the molecular interactions of the cytoskeleton and the extracellular matrix with the membrane. I now sense, however, that it was an audacious proposal to make at the time because there was so little evidence to support it. Although the basic features of the new membrane model were put forward in 1966 and I was convinced that the model was substantially on the right track, there was not much impact on the field until our 1972 paper in Science. I think that this is often the fate of new ideas, whose revolutionary features are not immediately recognized and widely accepted in the absence of a large body of supporting facts. In this respect, the immediate impact of the double helical structure of DNA, exploding full-blown, as it were, from the head of Zeus, is quite atypical of how new ideas become accepted. More typically, an idea is not so obviously correct at the outset, and a deep insight and an openness of mind are required of those who receive new ideas, as well as patience and courage of those who propose them. Of course, ideas can also be wrong, probably a great deal more often than they are right. Intuition and judgment are necessary to identify those ideas worth pursuing, qualities that I will not dwell on because they elude definition. What I want to stress here is that the fear of being wrong is a great deterrent to the advocacy of new ideas. Even wrong ideas, however, can sometimes be useful in science if, for example, they contain elements that are of interest in other connections (as, for example, in the case of Pauling's theory of antibody formation alluded to earlier) or if they serve to focus attention on the central features of the problems being addressed. Too much opprobrium attaches to wrong, as opposed to wrong-headed, ideas. Wrong ideas should be decriminalized. As I suggested earlier in this article, our science has become structurally less dependent on informing ideas. In a curious way, the approach of doing research without any prior conceptualizations, letting the collection of experimental results tell us what is going on, brings us all the way back to the precepts of Francis Bacon about how to do science by induction, as discussed in Vol. 3, April 1992

The New Atlantis. Our present problem, however, is not simply structural. There is in addition an active disparagement of ideas that is becoming widespread. This current takes several forms. Ideas are frequently labeled pejoratively as "speculation," and speculation is ruthlessly suppressed in our publications. It, sometimes seems as if our leading scientific journals have hired carefully trained copy editors whose primary function is to detect and expunge speculation from manuscripts, much as we now have trained dogs to sniff out plastic explosives in airport luggage. Referees have also learned this technique. Review articles, a proper vehicle for grand new ideas, have increasingly become simply compendia of results and citations, rarely extending ideas a micrometer beyond the facts. New journals, "Trends in. . ." and "Current Opinion in. . .," have been specially produced that segregate and confine speculation within appropriate institutional bounds where they can be largely ignored. Why is all of this a problem if, as everyone agrees, the current Baconian practice of much of molecular cell biology is highly productive of new information? There are several reasons to be concerned. For one thing, the molecular genetic approach doesn't always work or give the complete answer. This is nowhere better revealed than when, after a long series of experiments, a gene product is implicated in a particular process that turns out to have no known homologue in the protein data banks. Rather than this result being a source of great rejoicing, because clearly one has come upon something entirely new, it is instead a source of despair and a dead end. For another thing, no one knows how long current approaches will remain successful. Eventually, a great number of genes will have been cloned and many proteins will have been implicated in each particular cell function. It may then be necessary to formulate new ideas about how to integrate all of this complexity into some coherent schemes. Ideas are therefore not really dispensable, even if they appear to be largely so temporarily. If formative ideas are, and will continue to be, necessary, we need to be concerned about encouraging their generation. I have remarked earlier that ideas do not come out of the blue; they arise in individual minds from associations made with ideas and facts often derived from other research areas. Such associations are fostered by a breadth of experience and knowledge. On the other hand, the training and experience of our scientists, by the very nature of our science, are becoming narrower and more focused on specific subjects. It will not be at all unusual for an investigator in the near future to spend his or her entire research career on a single, rather confined, problem. The investigator will publish in, and read, only more and more specialized journals. For those scientists who would chafe under such severe and unavoidable strictures, a number of positive steps have to be taken so as to escape this in387

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tellectual straightjacket. As an undergraduate, for example, the future molecular and cell biologist should become familiar with a wide range of scientific subjects, and in particular, with physical chemistry and thermodynamics. In all of the student's future career, he or she will be continually dealing with molecular structures and molecular interactions, problems that can only be understood in physical chemical terms. Even now, however, many molecular cell biologists are ill equipped with respect to physical chemistry. Graduate students and postdoctoral fellows could help their situation through regular attendance at seminars covering a wide range of subjects, so as to encounter the thrust of unfamiliar ideas and research areas. A universal complaint today, however, is the poor attendance at seminars other than those given by a few superstars. One goes only to those seminars directly relevant to one's research. Here, faculty mentors should provide an example to their younger colleagues but often do not. Graduate students would also do well to select Ph.D. mentors, not so much on the basis of who is doing the "hot" science of the day, but who is interested as well in ideas and in a diversity of research problems. Those who eventually join a university faculty are in a particularly fortunate position to expand their horizons. Even if their own research activities have to be narrowly confined, they have the marvelous opportunity to teach a wide range of subjects. By far the most effective way I have ever learned a subject was to teach it. One can, of course, learn things by means other than teaching them, but never as crisply and coherently as when one has to convey them to hundreds of students for an entire term, year after year. The 10 years I spent teaching undergraduate physical chemistry in my first faculty position at Yale, 3 hours a week for the entire academic year (in addition to 3 hours a week of Freshman chemistry and laboratory), forever imprinted physical chemistry and elementary thermodynamics in my brain. This comprehension eventually provided the basis for my ideas about membrane structure and still informs everything I do in cell biology. When I joined the Biology faculty at the University of California at San Diego, I began to teach a graduate course in physical biochemistry. I had to learn about optical rotatory dispersion and circular dichroism, recent developments that I knew little about. I learned these so well that I saw how to use these methods to initiate our experimental studies of membrane structure (Lenard and Singer, 1966). In my years at the University of California at San Diego, I have taught at the undergraduate and

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graduate levels full courses in biochemistry, cell biology, immunology, and membrane biology, all of which consolidated my understanding of these broad areas as no other experience could have done. Such firm understanding was of central importance in fostering our research in all of these areas. It is therefore unfortunate that this kind of teaching experience generally escapes those who work at research institutes or those who are on teaching faculties but insist on teaching only in their narrow areas of research specialization. One does not have to be an expert in a given area to teach an undergraduate course. A good textbook and some effort are all that it takes to begin. The idea that teaching is strictly a burdensome activity that serves only to detract from one's research productivity is one of the most misguided notions of our time. This notion not only does a disservice to the individual researcher and teacher but contributes to an unhealthy collegiate atmosphere in which teaching and learning are too often viewed as little more than chores. Finally, and perhaps the most important thing I can say about ideas is this: nothing has ever given me as much gratification and sheer pleasure in science as having a first-rate idea. Such ideas may have been few and far between, but they have left the deepest impression on me. I have no fonder wish than that the same kind of satisfaction is achieved by coming generations. REFERENCES Kauzmann, W. (1959). Some factors in the interpretation of protein denaturation. Adv. Protein Chem. 14, 1-63. Lenard, J., and Singer, S.J. (1966). Protein conformation in cell membrane preparations as studied by optical rotatory dispersion and circular dichroism. Proc. Natl. Acad. Sci. USA 56, 1828-1835. Pauling, L. (1940). A theory of the structure and process of formation of antibodies. J. Am. Chem. Soc. 62, 2643-2657. Pauling, L. (1986). Early days of molecular biology in the California Institute of Technology. Annu. Rev. Biophys. Biophys. Chem. 15, 1-9. Pauling, L., and Corey, R.B. (1953). A proposed structure for the nucleic acids. Proc. Natl. Acad. Sci. USA 39, 84-97. Singer, S.J. (1962). The properties of proteins in nonaqueous solvents. Adv. Protein Chem. 17, 1-68. Singer, S.J. (1971). Molecular organization of biological membranes. In: Structure and Function of Biological Membranes, ed. L.I. Rothfield, New York: Academic Press, 145-222. Singer, S.J. (1974). The molecular organization of membranes. Annu. Rev. Biochem. 43, 805-833. Singer, S.J. (1990). The structure and insertion of membrane integral proteins. Annu. Rev. Cell Biol. 6, 247-296. Singer, S.J., and Nicolson, G.L. (1972). The fluid mosaic model of the structure of cell membranes. Science 175, 720-731.

Molecular Biology of the Cell

Ideas are becoming an endangered species.

Essa Molecular Biology of the Cell Vol. 3, 385-388, April 1992 Ideas are Becoming an Endangered Species S.J. Singer Department of Biology, Universit...
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