The Human Genome Project: Mediocre Science, Terrible Science Policy
In this tract, circulated mostly to influential scientists such as Anfinsen, Professor Rechsteiner of the Department of Biochemistry
at the Utah School of Medicine urged others to contact influential law makers to limit or cut funding to the Human Genome
Project, which Rechsteiner believed had questionable medical and scientific value.
Item is a photocopy.
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Reproduced with permission of Martin Rechsteiner.
Medical Subject Headings (MeSH):
Human Genome Project
Letter from Christian B. Anfinsen [re: value of the Human Genome Project] (March 27, 1990)
The human genome project: mediocre science, terrible science policy.
Few scientific proposals have been greeted with as much media coverage as the human genome project. This is understandable
since humans are a narcissistic species, and the thought of knowing their molecular blueprints in detail might appear exciting
to many. Unfortunately, the human genome project (HGP) is not a sound scientific undertaking. Moreover, in a period of severe
budget restraint at
the National Institutes of Health, it is foolish to invest three billion dollars (or more) to sequence the entire human genome.
Below, I briefly discuss five reasons for thinking the HGP is an ill-conceived idea. Despite an abundance of articles on
the HGP and ample reference to its critics, the basis for their opposition has not found its way into print. I hope this
letter contributes to an increasingly vocal
opposition to the project.
The HGP has questionable origins.
This statement may sound like back-fence gossip, but it is meant to convey the fact that the HGP did not arise from a broad
consensus that the sequence information was badly needed. Rather the idea seems to have emanated from somewhere at the Department
of Energy; most evidence points to the deserts of New Mexico. Formally, the idea was presented by Charles DeLisi (1); a bill
to fund the HGP was subsequently introduced by New Mexico Senator Domenici (2). This led to a squabble over which government
agency, DOE or NIH, should direct the project. Sadly, the NIH won adding an air of medical legitimacy to the venture. Had
DOE prevailed, I believe we would see much more vigorous opposition from the biomedical and biological community. As it is,
I believe an overwhelming majority of the latter consider the HGP a bad idea.
The HGP has questionable goals.
The original aim of the HGP was simple enough. Determine the sequence of all the base pairs in the human genome. Never mind
that 95% of the DNA doesn't code for proteins and is thought by many, including some of its advocates, to be "junk"
(1). The goal has shifted recently to include sequencing of plant, worm, yeast and bacterial genomes as well (3,4). This
move, reminiscent of political maneuvers by defense contractors to spread manufacturing among several states, has generated
a few more enthusiasts for the project. But as noted above, I believe that most U.S. bioscientists do not support brute force
sequencing of genomes.
What is the justification for all of this sequencing? We are told that the resulting information will have great impact on
major human diseases. This is a specious argument for several reasons. First, significant advances in understanding the two
major diseases in the U.S., heart disease and cancer, were made independent of the HGP. The seminal work of Brown and Goldstein
on cholesterol metabolism did not require their knowing the map positions of HMG Co A reductase or the LDL
receptor. Likewise, most oncogenes have revealed themselves by their dominant effects, not by sequence analysis of human
Second, even the two stunning successes of the human mapping approach, discovery of the genes responsible for cystic fibrosis
and muscular dystrophy, did not require detailed sequence information. To be sure, a reasonable linkage map was needed to
identify the CF and MD genes, and I support continued refinement of the human genome map. But a map was available and was
being refined in the absence of the HGP. It would be far better to target specific diseases using a better human genetic
map than to sequence yards of DNA on the chance that a medically important locus is present.
Third, knowing the map location or amino acid sequence of a mutant gene product does not ensure the development of rational
therapies. The amino acid sequence and even the detailed X-ray structure of the RAS product have been known for several years
(6). Yet, treatments based on these advances remain to be developed. The recent finding that inhibitors of mevalonate production
the tumor-promoting actions of RAS may be such an advance (7), but all of these results came without a human genome sequence!
Clearly, structural information is important, but it must be accompanied by insights into the physiology and cellular functions
of the various gene products. This requires national support for many scientific approaches, which brings me to the next
The HGP is a costly wasteful and inappropriate allocation of research funds.
Its boosters say that the HGP will cost $200 million per year for 15 years. This three billion dollar total assumes, of course,
no delays and no cost overruns. But already we are apprised of delays in the project (8). How do we know it will only take
15 years? And what response could be raised at that time to a claim that "we're only half-finished?" The open-ended
nature of the venture is disturbing. The HGP may become the first NIH project to compete with defense's C5A transport
as a drain on federal coffers.
Of this projected three billion dollar outlay, Cantor estimates that 20% will be used for computer databases alone (9). Imagine
that! Six hundred million dollars to computer-warehouse junk DNA sequences. Apparently, the rest of the money will be disbursed
to several sequencing centers, to companies for developing sequencing equipment and perhaps to a few individual labs. The
thrust is big science, not small science, so no doubt most of the cash will go to centers and/or industry.
Watson is quoted in Science as saying "Two hundred million dollars is not all that much money" (10). Clearly, that
is a matter of opinion. Granted, it is not a lot of money by defense department standards. Perhaps that was Watson's
frame of reference since so much about the HGP smacks of defense department mentality. As one of a large number of PI's
with a current NM priority score between 10 and 15%, I can assure Watson that 200 million dollars seems like a lot of money
For a struggling young assistant professor facing tenure, it might appear to be all the money in the world. However, the
key issue is not one's perception of wealth, but whether $200 million should be disbursed as 1000 RO1 grants, thereby
funding laboratories in universities, or as 10 or so block grants to sequencing centers. For me, there is simply no doubt
the proper choice. is the former.
The HGP will provide little useful training and no intellectual stimulation to young: scientists.
Headline in the January 8 issue of The Scientist -- "Researchers, discouraged by mapping's drudgery, doubt that a
five-year plan to finish high resolution image is now feasible." If mapping is drudgery, what word applies to sequencing?
Because the HGP provides so little intellectual excitement for graduate students or post-doctoral fellows, it will be accomplished
by technicians. Two hundred million dollars translates into 1,000 RO1s that support a diverse collection of undergrads, graduate
students and post-doctoral fellows at various universities. Besides the actual scientific product from these grants, there
is a tremendous educational benefit to the nation. By contrast, diversion of the same funds to the HGP will result in armies
of technicians skilled only in obtaining DNA sequences and entering the results into data bases. At a time when a scientific
career looks bleak enough, it makes no sense to compound the problem of recruiting scientists by restricting university grants.
Since the future of U.S. biomedical research depends upon vigorous training programs, it is bad science policy to fund cadres
of technicians at the expense of university laboratories.
The HGP is divisive.
The concept of big science versus little science, new to biology, is frankly quite distasteful. The words conjure up big leagues
versus little leagues, serious versus trivial, important versus unimportant. True, these terms have long been applied to physics
where they apparently do not cause rancor. The same cannot be said of their recent introduction into biology. It has been
proposed that big science is
bad science (11). The spirited debate that followed on whether big science, defined as 20-30 post-docs per lab, is anywhere
near as efficient as the typical smaller research group takes on a whole new dimension when applied to the HGP.
The HGP can be curtailed.
Those in power always promote the idea that you cannot beat city hall. I do not believe that. The demise of Mohole, a similar
grandiose, costly and ill-conceived project to drill deep into the earth, proves that bad ideas are not inevitably implemented.
If there are enough concerned biologists willing to write letters to key congressmen and administrators, we can curtail the
HGP to a more reasonable and useful mapping project. If you agree with the arguments presented, then write Science Advisor
Allan Bromley, NIH Acting Director William Raub, Senator Gore or Senator Kennedy and express your reservations, concerns or
opposition to the HGP. Their addresses are:
D. Allan Bromley
Science Advisor to the President
360 Old Executive Office Bldg.
1700 St. & Pennsylvania Ave., N. W.
Washington, D.C. 30506
Senator Al Gore
United States Senate
Washington, D.C. 20510
William F. Raub
National Institutes of Health
Room 126, Building 1
9000 Rockville Pike
Bethesda, MD 20892
Senator Ted Kennedy
United States Senate
Washington, D.C. 20510
In short, the HGP is a waste of national resources and is detrimental to the training of young scientists. I urge you to
take the time to voice your opposition --5,000 letters would have a significant impact.