Yes: It Bureaucratizes, Politicizes Research

When techniques for sequencing segments of DNA became available, it seemed self-evident that the most valuable material to analyze was the regions that could be associated with a function or a disease. More than 95 percent of the human genome did not seem interesting to explore in detail because it does not code for the kinds of functions that we can recognize, and so it is temporarily called "junk." A few years ago, however, it was proposed that systematic sequencing of the entire human genome was now feasible and should be regarded as a major challenge. This human genome program had an unusual origin. It was not initiated by a committee of molecular geneticists dealing with a pressing need, or by the major biomedical funding agency, the National Institutes of Health. Instead, it was advanced by an administrator in the Department of Energy, convinced that with the powerful tools of molecular biology it was now time to introduce centrally administered "big science" into biomedical research. The idea quick-ly developed strong political appeal. Sequencing the entire human genome was as definite and as highly visible as putting a man on the moon; it promised large benefits for human health and for our understanding of human biology; and it was claimed to be more efficient and cheaper than reaching the goal eventually by piecemeal sequencing. The NIH was initially not supportive, but when the program proved to be inevitable, it became the logical major partner. The HGP has now acquired a distinguished leader and set of advisers, and funding has grown rapidly. Meanwhile, two important changes have led to growing concern in the biomedical research community, building on an initial uneasiness about starting "big science" in their area. First, recent cuts in the funding of grants in other areas have drawn attention to the problem of competition from the HGP. Second, within the HGP the aim of starting to sequence the human genome has been replaced by a very different plan; and even though much of this involves kinds of work that would be going on even if there were no HGP, the program has inherited a high level of support, and a centralized mechanism of funding, from the initial plan. These changes suggest the need to reevaluate the HGP. Since concern over competition of the HGP with other research funding has focused primarily on the NIH, the issue might be considered beyond the purview of a committee examining the DOE. But the two parts of the HGP are closely intertwined in their goals, and a broad perspective on how best to fund biomedical research would have to take both into account. NIH study sections consider two kinds of investigator-initiated applications: new projects and "competing renewals," that is, applications for renewal of grants whose committed period has expired. Within the past few years the combined number of such grants funded annually has fallen from over 6,000 to 4,600; and among the total grants approved by study sections, the fraction funded has fallen from more than 40 percent to less than 25 percent. Indeed, some institutes have dropped this year to 15 percent or less. Study sections thus face the depressing prospect of virtually tossing a coin to choose among scientists with a continuing record of distinguished achievement, and promising beginners are even more at risk. While many factors contribute to the changing numbers of grant awards, there is without question a real decline in the support of research, with appropriations failing to keep pace with increases in its cost and in the number of excellent applications. The conclusion seems inescapable that far too many excellent scientists are not being funded. The consequences are far-reaching. Apart from the valuable research that does not get done, the continuity of the research enterprise, so essential for its effectiveness, is being disrupted. Moreover, bright students are being discouraged from seeking careers in science. The last effect is particularly important, at a time when the loss of interest of our youth in science, and their poor performance in international tests in science and mathematics, promise a continuing decline in our preeminence in science and technology. In principle the HGP should not be a part of the problem, for it was initially presented as an exciting opportunity for which Congress would be happy to provide additional money. But even though NIH officials maintain that the HGP is listed as a separate line item in the budget for biomedical research, the structure of that budget does not reflect the psychological elements that inevitably force Congress, especially in times of stringency, to focus most sharply on the total. It is thus hard to doubt that the HGP is competing with the initiatives of investigators in untargeted areas. And the scale of the potential competition is not negligible. The president's budget for next year recommends a total of $7,929 million for the NIH, with $943 million for new and competing grants (from which more than $60 million is targeted for grants for AIDS and the HGP) and $3,231 million for noncompeting grants. Hence, the future annual total for the HGP, $200 million, would be about 5 percent of the amount allocated by NIH for untargeted research in all areas of the biomedical sciences. The perception of competition on this scale is engendering bitterness in the research community. But a deeper cause for the concern is doubts about the scientific justification for the present scale and status of the HGP. First, many are not convinced that a crash program for analyzing the structure of genomes will advance either health or the life sciences for many years to come, as much as studies of specific physiological and biochemical functions and their abnormalities would. Second, in contrast to some areas of physics, which require extremely expensive facilities, biology does not have an obvious need for big science. Our country's spectacular success in this area has depended much on the remarkable social invention of wide support of independent investigator-initiated, peer- reviewed research. Many biologists fear that the precedent of the HGP will weaken this tradition. A third concern is more political. Should this country take on a disproportionate part of the cost of a worldwide scientific problem, especially when money for science has become so tight? And is there not the added risk of generating international resentment over our hegemony, rather than appreciation for our generosity? To judge these arguments we must consider the altered content of the HGP, and whether its different parts all need its centralized approach. When a National Research Council committee appraised the initial HGP in 1986, it recognized that starting to sequence 3 billion nucleotides, at a cost of more than $5 each, would be quite impractical. It recommended a very different program, which would postpone systematic sequencing for at least five years and would concentrate instead on several other activities. These included developing a map of identifiable short sequences, which would make it much easier to locate any new human disease genes or other genes; sequencing human DNA regions of interest; developing much more economical procedures for sequencing; developing systems for effectively storing and accessing the massive data; and studying the genomes of other organisms, ranging from E.coli to the mouse. These recent additions to the HGP are all scientifically sound. In particular, going beyond humans to other organisms makes a great deal of sense, because they can be used as experimental models for human functions and disorders, and we will need experimental approaches to solve the most challenging problems. Nevertheless, the extensive changes in the new HGP mean that it has moved far from an initial dream. Indeed, most of it, except for the centralized plan for mapping, differs only in mechanism of funding, and in scale, from what we would be doing if the concept of an HGP had never arisen. If these activities were to be proposed as a novel program today it seems doubtful that they could generate the strong political appeal of the original proposal. To evaluate the justification for the present program we must look at its major components separately. Mapping signposts along the road clearly will be very valuable. It will help to locate genes involved in various polygenic traits--including most diseases, as well as the interesting physical and mental traits of individuals. Moreover, because find- ing the locator sites for the map is not itself very interesting, this part of the HGP evidently requires a centralized, quasi-industrial organization rather than conventional grants aimed at more creative discoveries. However, decisions about its scale of support should recognize certain limits to its payoff. Most monogenic diseases are rare, and genes of other classes will probably be studied mostly in experimental animals, which seem unlikely to be mapped extensively. Of What Scientific Value? Another goal of the HGP, the systematic sequencing of the entire human genome (now postponed), presents deeper problems. First, even if future automation should bring the cost per nucleotide below $1, the effective storage and retrieval of the 3 billion units of information will also be costly, and the total final estimate of $3 billion and 15 years is very much a guess. A more fundamental question is whether identifying the last nucleotide in a human genome really has deep scientific value, apart from its public relations impact. Sequencing the much smaller genomes of a few viruses has been a gratifying milestone, but it has not obviously added a great deal to what had already been learned from the study of specific regions. It is even harder to see how a complete sequence could be useful for understanding the organization of the huge human genome: The dimensions are wrong, like viewing a painting through a microscope. In the genome, knowledge at these dimensions will be valuable only within its functional units, each constituting a short region--just as we need to know the complete sequence of the amino acids in a protein to understand its three-dimensional structure and function. It thus appears that the best way to understand the genome is to continue to identify the sequence regions that can be linked to function. For this purpose it is straightforward to proceed from a known protein to its gene. The reverse process is also effective: locating the gene responsible for a disease of unknown mechanism, by its linkage to known markers in the genome, and then using the sequence of that gene to help identify the mechanism of the disease. An increasingly refined map of the genome is making this "reverse genetics" much easier. In a third approach, blind sequencing of the genome can also discover new genes, by recognizing a sequence with the characteristics that suggest coding for a protein; but this is not an efficient process. On the average it would be necessary to plow through 1 million to 2 million "junk" bases before encountering an interesting sequence; and then finding its unknown function would also be difficult. To be sure, it may be necessary to start from sequences in approaching one of the largest challenges: identifying the unknown functions that almost certainly exist in much of the "junk" DNA. But the answers seem likely to come from detailed study, including experimental manipulation, of small samples of the genome; it is hard to see how knowing the whole sequence would help. For these several reasons it is perhaps no great loss that the goal of systematic sequencing has been postponed. When it is reevaluated, five years from now, it may well come to seem quite unimportant. Among the other activities of the current HGP, the research on techniques clearly overlaps with the goals of mapping and sequencing. However, the HGP mechanism of funding may give this research an unwarranted advantage over other kinds. Finally, the other major activity, sequencing of interesting regions in humans or in lower organisms, does not have any obvious need for centralized organization, or obvious justification for insulation from competition with other research. Although all the goals of the HGP, except for the complete sequencing of the human genome (now postponed), are clearly worthwhile, there is widespread concern over the present status and plans of the program. There are two reasons: its competition with other research funds at a time of financial stringency, and doubt that its scientific benefits justify its rapid expansion and its organization in the pattern of "big science." The dissatisfaction is clearly widespread: A large majority of my departmental faculty have endorsed for publication a statement very similar to this one, and with no dissenters. The HGP may therefore need reevaluation. In any such reevaluation there would be no difficulty in justifying a centralized organization for the mapping, and probably for the research on methods. However, it is not obvious that these activities justify support for the HGP at a level equivalent to about 5 percent of all other biomedical research. In this connection, a reevaluation should recognize that excessive competition by the HGP could interfere with reaching its own goal, because investigations in many areas of research can lead to DNA regions of interest. The fundamental goal is to understand the human genome and its products, and not to sequence the genome because it is there. A shift of funds from the HGP to the support of investigator-initiated research could advance this goal. Bernard D. Davis is Adele Lehman Professor of Bacterial Physiology Emeritus at Harvard Medical School.

Yes: It Bureaucratizes, Politicizes Research

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