Scientists Must Challenge Today’s Common Wisdom BY JOSHUA LEDERBERG The history of science is replete with successes achieved through repudiation of the common wis- dom. In the following, I offer some unconventional and speculative challenges to how we think about some large problems in contempo- rary biology. Most are not new thoughts, but to my knowledge they have not been refuted. I know they are mostly wrong; but I am not sure all are. They will surely be addressed, and most solved, during the next century. If I could foretell exactly how, I would be wasting no time getting to work on them in the laboratory. Eobiology. Conventional the- ory makes the origin of life a photo- chemical process of the early atmo- sphere of our own Earth. But the cosmic condensation necessarily involves preeminently light ele- ments, including hydrogen, carbon, nitrogen, and oxygen. The aggrega- tion of stars and planets is already an exercise in organic chemistry. Many large molecules have now been observed in space. Should we not look there for early chemical evolution, perhaps even of the rudi- ments of nucleic acids and proteins or their predecessors? Exobiology. The cost of radio receivers and of computation may finally be reaching an asymptote that would justify some modest in- vestment—if not now, in the next decade or two—in acquiring and processing potentially intelligent signals. We have no way to assess the probability of their occurrence. As to the solar system, the 1975 Viking mission gave a discouraging report on Mars; but it is wrong to foreclose the possibility of micro- habitat refuges—especially at mod- est subsurface depth—perhaps from a more hospitable epoch in that planet’s history. The thermal vents on our ocean floors offer an analogue of such habitats. The Epigenetic Dilemma. The central model of cellular dif- ferentiation must reconcile (a) the orderly delimitation of gene ex- pression in embryonic cell lineages, (b) the clonal inheritance of these self-sustaining differences, and (c) . the apparent reversibility of these effects in some stages. On account of (c), we usually as- sume the genetic uniformity of all somatic cells and, therefore, that 16 THE SCIENTIST July 11, 1988 LEADING QUESTIONS: Lederberg addresses the big issues. epigenetic cell changes are epinucleic—that is, they do not al- ter the primary informational se- quence of the DNA, but involve secondary structures or lateral at- tachments like methylation and histones. But, the dogma of genetic uniformity of somatic cells was overthrown with modern concepts of antibody formation. This is un- likely to be the only exploitation of nucleic diversification of somatic cells. Mechanisms of reversible nu- .cleic differentiations are now known in prokaryotes. Should we abandon the search for epinucleic explanations? I favor an eclectic perspective; but we have still to find a robust example and rationale of epinucleic transmis- sion. We seek a consensually ac- (Continued on Page 16) cepted experimental model, not just of modulation of gene expres- sion, but also of its quasi-stable in- heritance without nucleic alter- ation. The field might look for a Max Delbriick who would establish some discipline about the models to be pursued, as he did in plying phage T2 40 years ago. More attention also should be given to grossly obvious histologi-’ cal differentiation of nuclear and chromosomal structures: bands in polymorphs and dimples in mono- cytes must be epiphenomena of un- derlying chemical differentiation; and I will be rather surprised if they are not associated with fairly specific segments of DNA informa- tion and their current expression. The recent explorations of human fragile-X chromosomes show the value of correlating morphological and molecular-biological observa- tions. Aging. Here, too, we have yet to establish a consensus on what phe- nomenon we are investigating, on what would constitute an explana- tion. I suggest we use as a standard the difference in lifespan between human and mouse: Are there any cellular attributes that can be cor- related with that outcome? Cancer. The paradigm of the oncogene is properly taking hold, and I do not dispute it. Rather, I ask whether chemotherapy or ra- diotherapy can really be explained as solely responsible for eradication of all tumor cells. This seems very doubtful, and the collaboration of endogenous biological defenses must be-involved. If so, it has been mischievous to focus on modifiers like interferons or interleukins as sole therapeutic agents to be tested: as single agents. They must be ex- amined as adjuvants to cytocidal agents. Heart Disease. The HDL/ LDL (lipoprotein) ratio has been established as the best predictor of atherosclerosis. Almost no thera- peutic research is founded on ef- forts to modify this ratio, which is certainly a question of differential gene expression under metabolic regulation in the liver. Psychiatric Disease. Our only leads are (a) psychotropic drugs’ mode of action and (b) ge- netic influences in disease. We are beginning to see important studies on DNA probes for polymorphisms linked to disease susceptibility. However, almost no one is looking at polymorphism in psychotropic drug metabolism, although there are many clinical hints of it. This would reflect the handling of en- dogenous metabolites. Human Intelligence. Are we too wedded to the prewired switch- board model? There is abundant evidence for extensive cell migra- tion during development. Could this continue throughout adult life and be part of learning? There is recent evidence of cell turnover, at least in song nuclei in birds. Is hu- man cerebral function merely a nu- merical extrapolation of the neuro- biology of lower mammals, or are there higher orders of differentia- tion of neuronal types in the hu- man brain? If not, why is so much nucleic information uniquely ex- pressed in the brain? Physiology and Anatomy. That exercise influences muscle hypertrophy is an everyday ob- servation. To understand it and other banalities at 4 molecular level could have great practical applica- tion: not just for Olympic compe- tition, but for maintenance and re- habilitation of the heart and of that organ so uniquely vulnerable in the human, the intervertebral disk. To refer to “compensatory hypertro- phy” of muscle or any other organ as a response to functional demand is hardly to explain its mechanism. Toxicology. Toxic “side ef- fects” are no longer incidental in the process of adoption of new drugs, pesticides, and other chemi- cals—they are the central issue. Toxicology must be elevated from a stepchild of pharmacology to a cen- tral position in the health sciences, as one of the most important appli- cations of a fundamental molecular biological insight. Most of our ex- penditure on empirical toxicology is wasted; it would be better de- voted to mechanistic analysis of toxic effects, especially the interac- tion of exogenous chemicals with. oncogene mutation and expression. The paradigm of comparative toxicology would seek a basic un- derstanding of the similarities and differences of human responses to chemicals compared to other spe- cies. We can protect human health only by well-founded extrapolation from simpler models. Historically, toxic substances (metabolic inhibi- tors) had been central to the unrav- eling of metabolic pathways. The study of colchicine helped uncover tubulin; neurotoxins did the same for synaptic mechanisms. How. ever, metabolic inhibitors have been displaced by more sophisti- cated tools of microanalysis, tracer methodology, genetic lesions for pathway analysis, and the direct isolation of enzymes. These have left a generation only dimly aware of that history. Public Health and Epide- miology. We have no good alter- native to the blind clinical trial— - but this is devoid of mechanistic content. Therefore, it tests only the narrowest of hypotheses: the -effi- cacy of the specific treatment, con- ducted precisely according to the protocol. Its conclusions could be. quite misleading about the most minute variations, unless a sensi- tivity criterion can be established. . Parasitology. When I started compiling this list a decade ago, I felt it proper to press not only the humanistic importance. but the sci- entific excitement that would at- tach to intensified research on pro- tozoan and helminthic parasites. The World Health Organization’s Tropical Disease Research initia- tive, with financial support from many foundations, is now a global scientific network devoted to these problems. The effort still needs much more support, especially from governments. There is no doubt that the field will be one of the most challenging and effective for the application of the modern tools of molecular biology. Looking backward into the fu- ture, we are not so arrogant as to prophecy the scope and prove- nance of the global scientific effort of a full century. Compare 1887 with 1987, and recall how science grows exponentially! As to content, the surest prediction is that many of our firmest beliefs will be seen as crude approximations, evoking nostalgia, amusement, derision, or—worst of all—indifference, in the hindsight of 2087. Joshua Lederberg is president of The Rockefeller University in New York. The foregoing has been excerpted from “The Second Century of Louis Pasteur: A Global Agenda for Biomedical Research,” his keynote address delivered on October 5, 1987, on the occasion of the centenary celebration of the Pasteur Institute in Paris.