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• W2080592300 abstract "1980, the year that Christiane Nusslein-Volhard and Eric Wieschaus embarked on their Nobel Prize–winning screen for embryonic lethal mutants in Drosophila, in some ways marked the end of the Age of Beautiful Theories in biology, and the dawn of the Age of Ugly Facts (to paraphrase T. H. Huxley, whose view of a tragedy was “a beautiful theory murdered by an ugly fact” *Huxley, T.H. (1897). Evolution and Ethics (New York: D. Appleton and Company).). If Watson and Crick's double-helical model of the structure of DNA showed that imagination (with a sprinkling of data) could triumph over Nature, Nusslein-Volhard and Wieschaus's saturation mutagenesis showed that evolution can produce biological mechanisms of such unimaginable complexity that it would be useless, if not laughable, to try to intuit them a priori. Nature's imagination, it showed, usually far outstrips that of the human brain. The Awesome Power of Genetics combined with Molecular Biology had created a way to solve biological problems while making as few assumptions as possible, let alone having to construct hypotheses out of whole cloth. Günter Blobel proposed his astonishingly bold “Signal Hypothesis” together with David Sabatini in 1971, on the cusp of this paradigm shift in Experimental Biology. It was sheer conjecture, a pure product of imagination and intuition. It invited all the more criticism because it was pursued so doggedly during an era when an increasing number of cell biologists were resignedly and humbly trading in hypothesis-driven science and rat livers for a bottle of ethyl-nitrosourea and a plate of yeast. That Blobel had the chutzpah (as an adoptive New Yorker, the term is applicable even in his case) to advance such a speculative idea in the absence of any data struck many as the height of arrogance. That he clung so tenaciously to his theory during the many years when definitive experimental support for it was slow in coming invited caustic criticism. Papers claiming to have disproven his hypothesis dripped with Schadenfreude, condescending countertheories abounded, and his papers and grants were endlessly rejected. That in the end he proved to be right, in such an astounding degree of detail, was all the more galling and stupefying to his incredulous detractors. But this is not to imply that Blobel's talents and contributions were purely theoretical. To the contrary, he had an unflagging determination to experimentally test all the various predictions of his hypothesis, no matter how difficult this was to do. He inspired generations of students and postdocs to apply biochemistry, ion channel physiology and yes, even genetics, to find out whether the fanciful diagrams he and David Sabatini initially scrawled were actually true. Ironically, the first component of the translocation pathway to be discovered, signal recognition particle (SRP), was essentially the only major feature not envisioned in the original model: a soluble signal peptide recognition complex that arrests further translation of nascent polypeptide chains in the cytoplasm, and serves as an adaptor to couple the ribosome to the membrane-associated translocation machinery in the rough ER. The truly amazing aspect of all this is that a quarter century of experimentation by Blobel and his colleagues has over and over again validated the basic concepts of the original signal hypothesis: secretory and membrane proteins indeed contain short stretches of hydrophobic amino acids that target the polyribosomes synthesizing them to the rough ER, and in most cases these are at the amino terminus as originally predicted; there is a specific receptor for such “signal peptides”; and recognition of the signal peptide and docking of the polyribosome to the rough ER opens a proteinaceous tunnel in the membrane that facilitates translocation of the nascent chain across the lipid bilayer. Furthermore, the concept that variations in the number and the positioning of signal sequences within the polypeptide chain could be used to explain the “stitching” of membrane proteins of various topologies in and out of the lipid bilayer, laid out in another theoretical paper entitled “Intracellular Protein Topogenesis,” has proven largely correct as well. Finally this basic model, originally formulated to explain the targeting of secretory and membrane proteins to the rough ER, has proven to be extraordinarily global, and explains in principle how different proteins are specifically targeted to all sorts of intracellular membrane-bound compartments, including mitochondria, lysosomes, peroxisomes, chloroplasts, the Golgi apparatus, and the rough ER itself, to a degree that even Blobel himself did not initially fully anticipate. Those of us who studied with Blobel during the late '70s and early '80s recall the extraordinary amount of resistance he encountered in promulgating the Signal Hypothesis. Although such skepticism and disbelief was a constant source of irritation and frustration, it paradoxically provided critical emotional fuel to propel Blobel through those dry periods, sometimes lasting several years, in between experimental breakthroughs. “Tilting at windmills,” as Blobel colorfully described his fencing with critics and polemicists, kept him going and must make the sense of vindication he undoubtedly now feels all the more sweet. Blobel's Nobel, so richly deserved, should remind us how important different styles of scientific inquiry are to the success of the larger endeavor of a comprehensive human understanding of Nature. Blobel was and is an intensely human, passionate scientist who is deeply emotionally invested in his research. His theories were born of great leaps of intuition and imagination, rather than of the cold numerical calculations, formalistic deductive logic, or brilliantly exploited serendipity that have characterized other great scientific advances. Tackling such a complex problem as he did, initially without the benefit of any systematic approach, it is difficult to see how he could have succeeded in any other way. It is a style that is waning in Biology, and not only because the advent of the genomics era promises access to reams of data and exploration-driven rather than hypothesis-driven science. Perhaps it is also so rare because it is a style that requires a tremendous amount of psychic courage: the will to pursue an idea that may or may not be right. No one in science gets any points for proving their pet hypothesis wrong, even though this is often an invaluable step in advancing our knowledge. Yet, how infinitely less stressful and more secure to let the systematic acquisition of data drive one's science, especially when the baroque and counterintuitive biological mechanisms that evolution has produced so often mock the human imagination. This year's Nobel Prize in Physiology celebrates the fact that it is sometimes possible to solve hard problems just by thinking about them, if one is brave enough. Let us hope that it inspires some young biologists in the next generation to have the courage to do likewise. We will need their leadership.*Huxley, T.H. (1897). Evolution and Ethics (New York: D. Appleton and Company)." @default.
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