Cell, Vol. 65, 199-200, April 19, 1991. Copyright 0 1991 by Cell Press

What Will Be the Fate of Research on Prokaryotes? Many researchers presently studying our simpler organisms are deeply concerned about the future of prokaryote research, as interest in prokaryotes is noticeably shifting to other organisms. We believe that some journals no longer consider developments in prokaryotic biology worthy of reporting, and we fear that grant review panels may be giving undue preference to projects dealing with more fashionable experimental organisms. It also seems that university committees charged with selecting new faculty are favoring individuals engaged in research with eukaryotes because they feel that such studies are more likely to be supported. Do these perceived changes reflect the normal course of shifts of interest as new techniques expand our experimental capabilities and new knowledge is acquired? Are these changes desirable; will they enhance the future of biological research? Should we sit idly by and accept these changes, or should we alert the scientific community to their occurrence? The importance of these issues to the future of science has prompted my writing this editorial. (Once before I attempted to influence the course of biological research, that time to favor a better balance for eukaryotic research. In 1969 I was a member of a small group, sponsored by the Genetics Society of America, that obtained a grant from the National Science Foundation to consider the feasibility of initiating a national program on the molecular biology of the human cell. Our efforts were rewarded in 1972 when the National Science Foundation established a Human Cell Biology Program.) What is responsible for the apparent shift in research preferences? Clearly the application of recombinant DNA techniques and their descendent technologies has shortened the time from design of a research plan to completion of a project and publication of the results. These developments have also greatly expanded the range of tractable research problems. No organism is now beyond meaningful analysis of its genetic material. Genes or cDNAs can be cloned from all sources and, once cloned, can be manipulated with near equal ease. Microbial and eukaryotic hosts and vectors exist that can provide large quantities of precious proteins of animal, plant, and microbial origin; many of these proteins have exciting potential for medical and other applications. With modern technology expanding our capabilities, many of us face a difficult choicewhether to continue studying the unsolved prokaryotic problems that have been our principal concern, or to select projects in organisms that have just become amenable to experimental attack. For some the choice of organism and project will be influenced by the assumption that study of a new system or phenomenon in a fashionable organism will command greaterrecognition bythescientificcommunity-including members of grant review panels and editors of prestigious journals. Although young scientists have always been faced with the choice of research project and experimental organism, never before, in my opinion, has the decision been so sharply drawn between choosing an existing prob-

Editorial

lem, involving a prokaryote, versus one that appears to be new, in a eukaryote. This is not to say that the problems being studied in complex organisms are not exciting and important-they are, and truly spectacular developments are being reported daily in our seminars, journals, and newspapers. For the first time in the history of the biomedical sciences, it appears that every human abnormality or disease with a recognizable genetic component can be subjected to experimental analysis. And it may well develop that cloning and sequencing a human disease-related gene, and deduction of the function of the corresponding protein, will provide the most valuable clue to the molecular basis of the disease. This work must continue! But there are also many exciting and important unsolved basic problems, both old and new, that are best studied in simpler organisms. Since so many of nature’s common biological problems were solved during early microbial evolution, and since the solutions have persisted, is it not logical to investigate these phenomenawith the more convenient microbial model systems, as well as, or instead of, with more complex organisms? I would also argue that it is conceivable that many of the protein domains that perform the numerous catalytic, structural, and regulatory functions that all living cells require evolved first in prokaryotes and were subsequently tailored for specific functions by multiple genetic changes. These protein domains, inherited from prokaryotes, probably were used as such, or were shuffled to yield multidomain proteins with combinations of activities, or they were duplicated and copies were altered to allow performance of events that are relatively unique to eukaryotes. If this was in fact the course of molecular evolution, then studying specific protein domains in prokatyotes, where they can be most readily manipulated, would appear to be a sensible strategy. At a minimum, by determining how prokaryotic proteins perform their functions, we should learn how corresponding functions could be accomplished in eukaryotes. The same arguments apply to many eukaryotic processes that have counterparts in prokatyotes. We would all agree that prokaryote research has provided us with considerable knowledge and numerous concepts. Much of what we currently know about biological processes involving genes, proteins, and other cell components, stems from studies with prokaryotes. Browse through any textbook of biochemistry, genetics, or molecular biology and the rich legacy of these investigations will become apparent. And now, the powerful modern technology that has opened up eukaryote biology to exploration is also available for research with prokatyotes. The prospects for important discoveries with simpler organisms are excellent. Shouldn’t we do what we can to ensure that these discoveries will be made? In adopting personal research goals, one generally accepts the judgement of others as to which avenues of investigation will provide insight into important, unsolved problems and/or provide the basis for immediate.or eventual benefits to human health and welfare. Any problem

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that is new and experimentally approachable has particular appeal as asubject for investigation. However, I believe that the proper practice of science demands intellectual and experimental commitment until the process under scrutiny is thoroughly understood. We should discourage flitting from one project to another. More often than not, thorough analysis of an identified phenomenon has revealed new principles that were unsuspected. Our own studies on attenuation illustrate this point. It would be unfortunate if in planning for the future, new projects in eukaryotes were given undue preference simply because they were new. I believe that detailed, fundamental knowledge will always be required for sustained progress in the biological sciences. Recently I served on an NIH Study Section charged with reviewing research grant applications. The disheartening conclusion suggested by this experience was that our excellent peer review process was inadequate as a fund allocation procedure when only a small proportion of our outstanding applicants could be supported. Reviewers were forced to search for minor points to criticize so they could widen the range of priority scores. Evaluating a project proposal on a “new” topic in a eukaryote had an inherent difficulty. Except for the specific qualities of the object of the investigation-be it gene, protein, or process-each applicant invariably proposed applying state-of-the-art technology in his or her research. Assigning accurate relative scores to proposals based on these eukaryotic topics versus those based on prokaryotic ones proved virtually impossible. In my own laboratory, I am witnessing the contrasts between research on “old” prokaryotic projects versus “new” eukaryotic projects. Some members of my group are performing detailed analyses of transcription regulatory mechanisms in prokaryotes while others are exploring the regulatory “gold mines” of the organism I first worked with, the fungus Neurospora crassa. I find each of these problems exciting and challenging. But I usually derive greater satisfaction from the increased knowledge gained in the bacterial studies because it provides a more thorough understanding of the process under investigation. Many of you are aware that the Journal of Bacteriology has just begun publishing twice monthly. This change seemingly argues against the view expressed in this editorial, and suggests that there has been an increase in prokaryote research. Is this conclusion correct? Is prokaryote research truly flourishing? Sadly, I think not. I believe there has been a shift away from research with microbes. In my opinion, the increased burden being placed upon the Journal of Bacteriology is a consequence of the increased pace of modern research and the difficulty prokaryote researchers are experiencing in having their papers accepted by several of our most popular journals. I believe we have reached a crisis in recognition, support, and encouragement of microbial research. As new eukaryotic problems have come under investigation, both young and established investigators have switched their interests. Consequently, fewer research groups are continuing to analyze the significant problems for which prokaryotes are so eminently suited. Unless we are wary, the current state

of prokaryote research may soon extend to studies with yeast and Drosophila, as investigations with these organisms as well are deemed of only minimal value relative to what one can learn using mammalian systems. Should we not establish the principle that each project be judged on its intellectual or possible medical merits, with the primary importance of the species being its suitability for the investigation at hand? Despite the problems created by the dramatic increase in research project possibilities, and the attractions of eukaryote research, I believe that inadequate support for our current trained scientists is primarily responsible for the predicament we find ourselves in. Support for eukaryote research is poor, while support for prokaryote research is dismal. It is unlikely that we will succeed in our goal of recruiting bright youngsters into careers in science-all areas of science-if we do not provide adequate funds for those we have already trained. We must demonstrate that it is in the country’s best interest to provide the resources that will permit the scientific discoveries that will greatly improve our quality of life. Opportunities for scientific advances in the biological sciences have never been greater! We must show enthusiasm for all significant scientific contributions We must not downgrade ongoing prokaryotic research in comparison with new eukaryotic projects. The editors of our journals must be careful to consider the significance of the findings foremost rather than the topic of the research. Won’t we be doing a serious disservice to the future of our science if we decide arbitrarily that new projects in eukaryotes are most important, and reward only those who share this view? It is up to us to recognize the true value of scientific advances in all areas of biological research. Although I accept full responsibility for the content of this editorial, my colleagues Lucy Shapiro and Dale Kaiser contributed significantly to its development. I also thank Benjamin Lewin and Howard Gest for many helpful suggestions Charles Yanofsky Department of Biological Sciences Stanford University Stanford, California 9430.55020