The Case Against the SSC

I would like to lay out the scientific case against the Superconducting Supercollider because I think many of my colleagues who understand this case are hesitant to make it, not least because some of the arguments are two-edged. I am very hesitant myself, because I am not against the project, except insofar as it competes for resources which I see as needed more elsewhere. Let me organize my thoughts in terms of four slogans, each of which is aimed at sowing doubt about one of the myths supporti

By | June 1, 1987

I would like to lay out the scientific case against the Superconducting Supercollider because I think many of my colleagues who understand this case are hesitant to make it, not least because some of the arguments are two-edged. I am very hesitant myself, because I am not against the project, except insofar as it competes for resources which I see as needed more elsewhere.

Let me organize my thoughts in terms of four slogans, each of which is aimed at sowing doubt about one of the myths supporting the unique value of elementary particle physics.

  1. Science can be fundamental without being irrelevant.
  2. Money is important, but manpower and education are more so, and money affects these.
  3. The term "spinoff" should be erased from the language.
  4. The golden eggs are very seldom produced by the golden geese.

1. The first slide in many general talks given by my colleagues in high-energy physics is a length scale spreading from the "Planck length" (way below elementary particle size) to the size of the cosmos. They gesture deprecatingly toward the center of this scale (where we and our atoms and all of everyday life sit) and say, "Of course, we know everything there, and the only fundamental science is at extreme scales." Well, we don't know everything there. We haven't the foggiest idea what drives the new high-temperature superconductors, or what makes a snowflake, or how the mind or the economy works. What is more, nothing high energy physics can do will ever be of the slightest direct help in solving these overwhelmingly hard problems.

We have long since learned everything particle physics can tell us about the behavior of ordinary matter, even of nuclei, and probably of the stars themselves. If the particle physicists tell you they will understand even the Big Bang better as a consequence of the SSC, they are being wildly optimistic; and if they claim any other relevance, they are wrong. Their fundamental physics has become so "fundamental" as to be almost totally irrelevant, even to the rest of science.

2. Particle physicists have a way of comparing the cost of the SSC to that of a battleship or a missile and making it out as not very big on that scale. The catch there is that that much money spent on this kind of science is going to have a large effect on how we use our really bright, well-trained technical people, and on how we educate them. They are a resource that is extraordinarily scarce and getting much scarcer: so scarce that it is beginning to be a surprise to hear an American accent in the physics departments of this country, because we are having to fill in more and more with immigrants and visitors in our junior positions.

3. One of the great arguments for spending money on large technological projects is always the "spinoffs." One spinoff that is adduced for large accelerators is superconducting magnets. I was closely associated with the group at AT&T Bell Labs that invented these magnets in 1960, not as a spinoff from anything but as a consequence of a fundamental research program on superconducting materials, with no public funding and probably few prospects of getting any even then. Their further development was indeed carried out partly by wisely administered public money from the service agencies and partly by industry, and then by small instrumentation firms concentrating on scientific uses. So far as I know, the truly innovative part of this technology owes nothing to particle physics.

4. Those who manage the funding of science have a very strong prejudice in favor of large expensive projects and large unitary laboratories or centers. The amount of money available for free, unprogrammed individual research dwindles. Unfortunately, it is not the large, expensive programs that produce really new things. Of the last three major developments in superconducting materials, none of the breakthrough discoveries took place in the United States, the Chevrel materials being discovered in France and Switzerland, heavy electron superconductors in Germany, and high Tc oxides in Switzerland. Even once La2CuO4 appeared, the next confirmations appeared in Japan and then in Beijing. The materials themselves were primarily studied heretofore in India and in France.

This preponderance of overseas work is due in part to the poor funding of small science here, and in part to the channeling of what research we do into large facilities, which for the most part, are not places where you discover breakthroughs, or in which serendipity can operate. Rather, they are places in which you test breakthroughs once you have them. Innovative, small group work in this country must not be cut back in favor of the large facilities.

In conclusion, let me say that I too want to know what the ultimate structure of matter in the world is going to be, as well as how the Big Bang happened, and I want to see an accelerator going far beyond the present limits eventually built. I do not accept that doing so is as urgent as many other scientific needs of the country—in space science, science education, and above all in the rescue of our strong tradition of innovative, fundamental small science, which is now being carried on in only a few universities (such as Cornell), industries (such as Bell Labs) and government institutions (such as Los Alamos), all of which are in a somewhat embattled state. A fraction of the budget earmarked for the SSC could easily restore our prominence in this area, if given, say, to NSF and restricted to small science uses.

It disturbs me to see accelerator physics viewed as a nationalistic, competitive race; science is too serious a matter for that. And if the lack of the right accelerator here at exactly the right time is really going to kill high energy physics, I must say it is better off dead, if only for the crippling lack of imagination that attitude reveals.

In 1977 Anderson shared the Nobel Prize in Physics with John H. Van Vieck and Nevill F Mott. He is Joseph Henry Professor of Physics at Princeton University, Princeton, NJ 08540. This article is adapted from testimony before the House Committee on Science, Space and Technology on April 7 in Washington, D.C.

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