Notes from a Revolution: Lessons from the Human Genome Project

A critical scientific effort that almost didn’t happen illustrates the need for a rigorous but flexible process to evaluate large-scale transformative research proposals.

There are very few scientific endeavors that can be recognized almost immediately as seminal moments in the progress of human knowledge. The Human Genome Project (HGP) is one of them. There is no question now that the information locked in the DNA of all of us is both wonderfully rich in content and critically important to understanding biology and medicine.

The HGP, and the genomic revolution that it started, has become so much a part of biology that its history is often taken for granted. We have been surprised that many biologists and medical researchers are unaware that the initial proposal to sequence the human genome was fraught with controversy, that there was no clear consensus in the scientific community about whether it was worth pursuing. Opponents argued that funding the HGP would severely restrict investigator-initiated research projects, that we lacked the technology to complete the project in a reasonable amount of time, that the biological sciences would become increasingly politicized, and that even if it could be completed, most of the information would be useless. It was also argued that funding would be squandered on “big science,” and in the process the National Institutes of Health (NIH) and other science funding agencies would lose their focus and scientific effectiveness. All these objections might have seemed reasonable, considering the unknown future of science and technology as well as the tight research budgets, but in retrospect we can see that they were seriously misguided. A careful review of the origins of the opposition and the nature of their objections reveals the complexity of the science policy process, particularly for novel, large-scale projects.

When the project was first proposed in the mid-1980s, one prominent skeptic was Nobel laureate David Baltimore, who estimated that it would take 100 years to sequence the human genome, and many agreed. The 100-year estimate would, in fact, have been about right if the technology had remained frozen at the level of 1985. But the technologies used in sequencing the genome improved rapidly, and the century of work was compressed into 15 years. Another eminent geneticist, David Botstein, warned, less seriously, at a national meeting in 1986 against becoming involved in the “mindless big science of sequencing genomes,” to wide and warm agreement from the audience. To their credit, Baltimore and Botstein both quickly recognized the value of the project and were active in garnering support. They are examples of how good interactions and scientific debate in the community informed and built the case for the HGP even in the face of broad opposition. Others, however, remained irreversibly opposed.

Even as late as 1990, after more than four years of debate, and after the project had been formally proposed and received seed funding, the controversy continued to fester. Anxiety about the possible erosion of funding for individual research grants at NIH gave birth to a movement among university researchers opposed to the HGP. Martin Rechsteiner of the biochemistry department at the University of Utah sent a “dear colleague” letter to researchers across the United States urging a protest against the HGP as “a waste of national resources.” He was joined by many others, including Harvard University’s Bernard Davis, a well-known microbiologist. Rechsteiner and Davis testified against the project at a Senate hearing in July 1990 organized by Senator Pete Domenici of New Mexico and chaired by Senator Wendell Ford of Kentucky.

Davis argued that an organized project was unnecessary because the human genome would be mapped and sequenced by individual researchers working as they always had. The issue of taking money away from individual research grants at NIH was front and center, but Rechsteiner also expressed some disdain for what could be learned from the sequence of the genome. The hearing generated several letters and petitions from university departments opposed to the genome project that were included in the Congressional Record.

Nor was there a shortage of fierce objections to the project on scientific grounds. For example, Robert Weinberg, an eminent cancer researcher at the Massachusetts Institute of Technology, was one of a number of scientists who argued that the project made no sense since so little of the genome was used to code for proteins, and the data would likely reveal very little for the resources expended. An indication of the extreme end of this fringe came when Martin Rechsteiner told a New York Times reporter, “The human genome project is bad science, it’s unthought-out science, it’s hyped science.”

Had any of these arguments and attitudes prevailed—and they could have—they would have led us badly astray. Instead, we now have a rich resource whose scientific, medical, and economic impact has been transformative.

The project’s history has taught us useful lessons about the research process and about best practices for managing large, complex ventures and biomedical consortia. Some of the lessons were recently discussed by NIH Director Francis Collins and colleagues in an article in Nature. They outlined and briefly discussed six lessons, which emphasize the importance of partnerships, free data sharing, data analysis, technology development, and the ethical and moral issues that accompany all transformative technologies.

To these we can add two more: be flexible—because unanticipated difficulties occur in almost any complex project, and the organizational and financial structure must allow for these—and encourage multiagency participation. The success of the HGP was in no small measure the result of cooperation among a number of agencies, and especially between the Department of Energy (DOE), the birthplace of the project, and NIH, whose mission encompassed potential health benefits of the project. NIH provided an essential effort to address the medical implications, and DOE provided an equally essential piece that addressed the development of key technologies. The multiagency, international project quickly gained the attention of a diverse set of organizations and individuals and as such provided a context that, in retrospect, was unusually complex and nuanced.

Our focus here will not be on the scientific, medical, and economic importance of the HGP, since that is now widely accepted. Nor can we offer fixed prescriptions about how to proceed successfully into an unknown future. Instead, we reflect on science policy lessons that can be learned from the way the project was initiated, unfolded, and ultimately reached a successful conclusion.

We can’t help being struck by the fact that the genome project emerged suddenly from a background murmur of ideas and discussions, brought to life by DOE, a federal agency that was widely thought to be peripheral to biomedical science. This fact was in no small measure the source of considerable controversy and confusion. If large, complex enterprises become increasingly common in the future—as we might reasonably expect in this era of dramatic advances in knowledge, transformative technologies, and big data—and burst on the scene with little prior warning from an unexpected source, as the HGP did, it would seem wise to consider ideas and processes that might leave us better prepared than we were in 1985.

More specifically, many of our suggestions underline the importance of openness to new ideas originating from unexpected sources and the development of guidelines for considering large, transformative ventures that cut across multiple scientific disciplines and organizations. We briefly discuss the development of effective processes for public-private partnering and ways to accelerate transformative, inter-organizational projects. Some of our observations and ideas are now more or less accepted and have helped the nation find pathways to better science policy, but others have not yet penetrated our collective consciousness or operational policies.

The perspectives provided by the history of the HGP are brought into better focus when we recall some of the key cultural characteristics of biological research in the mid-1980s. First, there was relatively little discussion and interaction among agencies, even when their mission boundaries were somewhat blurred. Second, the culture of biology valued, almost exclusively, the small science of individual investigators. The HGP was viewed by many as an embodiment of wanton, brute-force science, light on knowledge seeking, devoid of hypothesis, and with no assurance of the biological significance of the eventual results. Third, application of modern technology and interdisciplinary effort had not yet become part of the general culture in biology. There were no large, complex, multiyear scientific projects in biomedical science that required contributions from multiple disciplines. Mathematics and computation, for example, were still largely foreign to the biomedical community, with the exception of statistical services for epidemiology, clinical trials, and some specialized areas, and much of technology development and engineering also stood well apart, though there were a few important exceptions.

Galas timeline

Lessons learned

The history of the HGP can usefully inform our approach to a wide swath of future science policy processes and help us avoid decisions that could lead to lost opportunities for the nation and the world, just as we nearly lost the opportunity to launch the HGP. The most important lessons include the following:

Remain open to new ideas, particularly those that emerge from unexpected sources. When a massive, decade-long, interdisciplinary project directly relevant to health sciences was proposed by DOE, the major funder of physics, chemistry, and engineering, the biomedical community was naturally surprised and somewhat skeptical. The National Institutes of Health, after all, was the world’s dominant supporter of biomedical science, with a long track record of major discoveries. But whereas NIH valued and focused almost entirely on the small science of individual investigators, DOE had decades of experience managing large, complex, collaborative projects that often required capital-intensive resources, including some related to health and the environment.

As DOE capitalized on its expertise in advanced computation and instrumentation to move increasingly into modern biology, its culture became fertile ground for the growth of a project such as the HGP. Of particular relevance is the fact that the only DNA sequence database had been established at the Los Alamos National Laboratory a decade prior to the start of the HGP.

Meanwhile, NIH was also beginning to accommodate proposals that were culturally aligned to what would become the substance of the HGP. Notably, it started to increase its support for biomedical programs that required intensive computation and large, biomedically inspired resource centers. These included new forms of mass spectrometry, the support of synchrotron X-ray stations at synchrotron particle accelerators for protein structural studies at several DOE national laboratories, and massively parallel supercomputing, all of which were starting to influence biological science and medicine. These winds of change, sweeping across the scientific landscape, were mostly unnoticed in biomedical circles.

Notwithstanding this neat and well-known division of responsibilities between the two agencies, DOE was no stranger to biology. The roots of biological research at DOE went deep, all the way back to the end of World War II. In 1946, just before the birth of the Atomic Energy Commission from the Manhattan Project, Eugene Wigner, a physicist at Princeton University and a Nobel laureate, was persuaded to take over Oak Ridge National Laboratory as director and to create a new kind of focused haven for scientific research. One of the first things he did was to hire Alexander Hollaender to build a biology division, in part to study the biological effects of radiation. Hollaender chose to build the research effort around genetics, and the study of the genetics of fruit flies, plants, and fungi became an Oak Ridge focus. In 1947 he hired William and Liane Russell from the Jackson Laboratory in Bar Harbor, Maine, to initiate a study of mouse genetics at Oak Ridge. By examining the genetic effects of radiation exposure, they soon discovered that the human exposure standards, which were based on fruit fly experiments, were far too high. The mice were more than 10 times more sensitive than flies to radiation mutations. For a while Oak Ridge was home to the largest biological research laboratory in the world, and it was richly productive. The Russells made a number of advances in mouse genetics, but there was much more. The division’s scientific credits include the discovery of the electronic nature of energy transfer in photosynthesis and Bill Russell’s seminal inference from genetic responses to the same doses of radiation exposures delivered quickly or slowly that a DNA repair mechanism must exist. Later on, in 1964, Richard Setlow discovered excision repair of DNA at Oak Ridge, and his student Philip Hanawalt subsequently worked out many of the implications of this seminal work. One of the most momentous accomplishments of the early era at Oak Ridge was the discovery of messenger RNA in 1956 by Elliot Volkin and Larry Astrachan (although they didn’t identify it as carrying the information from the DNA.) Nobel laureate Paul Berg said of this seminal experiment that it was an “unsung but momentous discovery of a fundamental mechanism in genetic chemistry,” and “has never received its proper due.”

Wigner also established a medical division at Oak Ridge, to focus more on medical effects than fundamental mechanisms. This sister division thrived as well, researching, for example, both the effects of radiation in inducing cancer and in treating it. One of the division’s luminaries, Arthur Upton, later became director of the National Cancer Institute.

The irony that DOE was positioned to initiate a genome-like project, largely by historic accident, actually reveals a deep principle worth noting. Preexisting diversity, created for any reason, can make transformations possible that might otherwise be unlikely. This echoes the themes of Darwinian evolution: diversification, selection, and amplification. At an organizational level, realization of this principle requires acute awareness, acceptance, and a philosophy fundamentally open to seizing unexpected opportunities for innovation.

The irony that DOE was positioned to initiate a genome-like project, largely by historic accident, actually reveals a deep principle worth noting. Preexisting diversity, created for any reason, can make transformations possible that might otherwise be unlikely.

Develop guidelines for vetting and responding to transformative ideas that cut across multiple scientific organizations and disciplines. Interagency partnering on large projects and strong lines of communication are now common. In particular, the National Science and Technology Council’s Committee on Science used by the Clinton, second Bush, and Obama administrations played an important role in coordination, especially in the neurosciences, and to an increasing extent in microbiome research, but its representation has tended to be focused on human health. Although participation could well be broadened, the helpful and encouraging voice of an organization such as the Committee on Science is a striking contrast to the profound silence that emanated from the Office of Science and Technology Policy, the executive branch’s central science and technology arm, when the HGP was launched.

This progress notwithstanding, the transformation is incomplete. The clear articulation of an inclusive vetting process for new and transformative ideas, and more focus on how to foster innovation, is still needed. And although interagency coordination on the HGP was established within only a few years of its inception, it happened in response to congressional influence and was contentious and far from optimal.

NIH was initially opposed to getting involved in the project, and its director, James Wyngaarden, was hesitant to move too far ahead of a divided community. Some of the key NIH advisers and several eminent scientists strongly advised Wyngaarden that NIH needed to support this effort on its merits and to assume its ownership, which had fallen to DOE by default because Senator Domenici had introduced a bill to start a national project under the aegis of DOE. Wyngaarden eventually agreed to support the HGP, and several congressional friends of NIH—notably Senator Edward M. Kennedy of Massachusetts, chair of the Senate Committee on Labor and Human Services, and Senator Lawton Chiles of Florida, a member of the Senate Appropriations Committee and chair of the subcommittee responsible for NIH—were mobilized to deal with Domenici’s bill. Early in 1987, Wyngaarden endorsed the HGP officially in congressional testimony. Domenici’s measure was soon absorbed into an omnibus biotechnology bill that died in committee. Finally, the start-up funds were appropriated to both NIH and DOE for human genome research in fiscal year 1988. The interagency Human Genome Project was born.

Develop effective processes for public-private partnering. Although interagency coordination is now much stronger than it was four decades ago, meaningful partnering and collaborative mechanisms need more development beyond the government. In the early genome era, there was one example of public-private interaction that stood out. The Howard Hughes Medical Institute (HHMI) played a critical catalytic role by engaging a number of key scientists in discussions. For example, James Watson met regularly with George Cahill, director of research for HHMI. HHMI also funded a number of meetings involving university scientists and people from several government agencies to discuss the issues surrounding the initiation of a genome project, and it provided initial funding for genetics databases, including OMIM, a continuously updated catalog of human genes and genetic disorders and traits. We are unaware of any organizations that encouraged regular communication, collaboration, and mutually beneficial partnerships among private enterprises, nonprofits, and academia, or any mechanisms to enable it.

In this brief essay we cannot begin to analyze the complexities and potential problems in partnerships between the government and for-profit organizations, but there is much potential to be gained in forming such partnerships. In the past few decades limited partnerships at the level of individual scientists from all sectors have become possible and are flourishing, whereas 30 years ago collaboration between a government scientist and an industrial researcher was routinely disallowed. Solutions to this problem evolved naturally as the benefits were recognized. A problem that has yet to be solved is routine and timely access to data, but its importance has been recognized. Many scientists, us included, believe that data generated at public expense should be released without significant delay, after quality assurance. This is relevant to for-profit organizations, universities, and nonprofits as well. Forty years ago, universities were not in the habit of patenting their intellectual property or spinning off new ventures, as they are now under the influence of the Bayh-Dole Act. As this trend continues, the pressure to sustain periods in which data are proprietary may also increase. We raise these issues to emphasize that considerable thought and attention is required in order to enable and encourage socially beneficial practices among all research institutions.

The private sector played a significant role in the HGP, including the development by Applied Biosystems Inc. of the automated capillary DNA sequencers that eventually generated the data for the first human genome sequence. Without this technology, it would have taken many more years to generate the data.

Whereas collaborations among scientists in different sectors should certainly be encouraged, as should collaborations among groups that provide complementary expertise, there are occasions in which parallel competitive efforts are useful and perhaps inevitable. The history of the HGP provides an example of the importance of such a parallel effort, although the way it played out was far from optimal.

Perhaps the most important industry role in the HGP was that of Celera, a private company led by J. Craig Venter, which was a key part of the end game of the project. Although there were ultimately two genome projects—one public (NIH and DOE), including international efforts, and one private (Celera)—there was substantial mutual benefit. The Celera effort was initially seeded by DOE’s Office of Health and Environmental Research, but the effort was organized, funded, and led independently of the public project, though many scientists with long involvement in the project contributed by joining the Celera effort or becoming advisers. In retrospect, the HGP is not likely to have been completed as early as it was without the massive effort by Celera using some newly devised methods.

There was significant disagreement within the scientific community about the relative merits of the systematic mapping and sequencing effort adopted by the public project and the “shotgun” sequencing and subsequent assembly approach followed by Celera. The stimulus to the federal effort provided by an independent private effort was, in our view, substantial. Ultimately, the initial reference genome, to which both contributed, was released sooner and with more data than would have been the case with either working alone.

Although there were specific criticisms made of each team by the other, it is now clear that both strategies worked. The overall goal of providing a huge amount of useful genome data to the community in a short time was greatly served by the parallel efforts. Finally, we must note that one of the general hallmarks of good science is an effective balance between competition and collaboration. The HGP demonstrated that this is possible, if difficult to achieve, even when it involves multiple complex organizations.

Develop a process that could move quickly to evaluate and establish large, transformative inter-organizational projects. It is worth considering where large, transformative projects come from. In all cases, ingredients include advances in science and technology as well as advocacy by a critical number of scientific leaders. Beyond those, the flame might be lit by an agency (as with the HGP) or fueled by conflict (the Manhattan Project), or by a combination of both (the space program) or perhaps by an unanticipated global crisis. A general process for casting a wide net and for soliciting, triaging, vetting, and facilitating the development of potentially transformative ideas across the biological science spectrum is worth developing. Perhaps the National Academies of Sciences, Engineering, and Medicine could play a significant role in this important process.

The NIH Roadmap is a possible model for soliciting, vetting, and initiating large, innovative, and potentially high-impact research projects that could be scaled up to an interagency level. The Roadmap solicits innovative trans-institute proposals that are then subjected to a multistep vetting process. To be applicable to science fields beyond the biomedical, however, it would need modification to account for the different community cultures and government agencies involved. Precisely how that could be done is well beyond the scope of this article, but we believe that what we have learned from the HGP may hold significant value for such future plans. In any case, clarity of purpose, faith in the creative resourcefulness of the scientific community, and a rich diversity of ideas has significant value for large, ambitious projects. Indeed, perhaps the most important lesson from the success of the HGP is that the scientific community’s creativity, organizational skills, and ability to cooperate and solve seemingly impossible problems should never be underestimated.

The NIH Roadmap is a possible model for soliciting, vetting, and initiating large, innovative, and potentially high-impact research projects that could be scaled up to an interagency level.

It is obvious that cooperation at all levels—among individual scientists, among consortia, among federal agencies whose missions have sometimes blurred boundaries, between the public and private sector, and among nations whose interests were not always fully aligned—contributed to the success of the HGP. Considering the rapidity with which the project came to the scientific and political arena, some trauma is not surprising. What is remarkable in retrospect is the boldness of the project, and even more, the rapid adaptation and cooperation by a biomedical research community that was traditionally conservative, by very different government agencies, and by a Congress with tight budget constraints. Its success is perhaps a good example of the mysterious wisdom of crowds, interacting openly. The strong cooperation that developed between NIH and DOE was essential to the testing of ideas, the fading of opposition, the marshaling of essential resources, and the strong support of Congress. The result was a remarkable contribution to human knowledge, a practical success and an example of a complex set of interactions that almost didn’t happen, but then really worked. The lessons of the HGP may usefully inform current efforts such as the Precision Medicine Initiative and the Cancer Moonshot.

A lesson that should not be drawn from the HGP experience is that every big, bold idea deserves support. The mechanisms that we propose to facilitate action on good ideas will also be useful in marshaling the rigor and insight needed to protect us from pursuing bad ideas. Open debate among experts from many disciplines, across federal agencies, and from many sectors of the economy is the best way to filter out the weak proposals as well as to build the foundation for cooperation on the most promising.

David J. Galas is principal scientist at the Pacific Northwest Research Institute in Seattle, Washington; Aristides Patrinos is New York University Distinguished Industry Professor of Mechanical and Biomolecular Engineering; Charles DeLisi is the Metcalf Professor of Science and Engineering at Boston University. Each of the authors served as director of biological and environmental research at the Department of Energy during the initiation and operation of the Human Genome Project.


Recommended reading

G. Cahill and D. R. Hinton, “Howard Hughes Medical Institute and its role in genomic activities,” Genomics 5, no. 4 (1989): 952-954.

E. Green, J. A. Watson, and F. S. Collins, “Human Genome Project: Twenty-five years of big biology,” Nature 526 (2015): 29-31.

Daniel J. Kevles, “Big Science and Big Politics in the United States: Reflections on the Death of the SSC and the Life of the Human Genome Project,” Historical Studies in the Physical and Biological Sciences 27, no. 2 (1997): 269-297.

E. Lander, et al., “Initial sequencing and analysis of the human genome,” Nature 409 (2001): 860-921.

National Research Council, Mapping and Sequencing the Human Genome (Washington, DC: National Academies Press, 1988).

S. Tripp and M. Grueber, “Economic Impact of the Human Genome Project,” Battelle Memorial Institute (2011).

Robert A. Weinberg, “The case against gene sequencing,” The Scientist (16 Nov. 1987).

J. C. Venter, et al., “The Sequence of the Human Genome,” Science 291 (2001): 1304-1351.

E. Zerhouni, et al., “The NIH Roadmap,” Science 302 (2003): 63-72.

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Cite this Article

Patrinos, Aristides, Charles DeLisi, and David J. Galas. “Notes from a Revolution: Lessons from the Human Genome Project.” Issues in Science and Technology 33, no. 3 (Spring 2017).

Vol. XXXIII, No. 3, Spring 2017