By Freeman Dyson (1988)

1. THE THIRD WORLD

I begin with three cautionary tales, one from each of the three worlds into which our planet is divided. These tales will have various morals. One of the morals is that human nature is the same in all three worlds. We are the same people making the same mistakes, whether we happen to belong to the third world, the second world, or the first world. But let me tell you the stories first. The stories should speak for themselves. After you hear the stories you can decide what the morals ought to be.

To represent the third world I choose the village of Ngon, a village in Central Africa where my daughter Mia spent some time as a Peace Corps volunteer. My information comes from an unpublished report which Mia wrote after she came home. Mia visited Ngon as an employee of the Of fice of Community Development of the Republic of Cameroon. Her official function was to assist and encourage local initiatives leading to the improvement of public health and education.

The main problem in Ngon is water. The village is several kilometers away from the nearest source of potable water. Night and morning, the women of the village must walk to the spring and back, with heavy waterpots balanced on their heads. During the dry season the spring degenerates into a muddy swamp. In 1985 the official Committee of Village Development, composed of prominent residents of Ngon and three neighboring villages, met to consider the problem of water supply. The meetings were conducted according to the traditional rules of African hospitality, the village chiefs presiding, their wives keeping the delegates supplied with food and drink, my daughter as an honored guest seated among the chiefs. The villagers mostly belong to the Boulou tribe and have their own Boulou language, but they have been educated for three generations in French bureaucratic jargon. The Committee of Village Development, in keeping with its official status, conducted its deliberations in French.

Two courses of action were available. I will call them Plan A and Plan B. Plan A was to engage the services of a professional well digger who happened to live nearby. The fee he charged was high by village standards, but not prohibitive. He would design and direct the construction of an adequate well, including a bathhouse and laundry, using the villagers as his work force. My daughter had made enquiries about his work in other villages and found that the results were generally satisfactory. Plan B was to write a formal proposal to the central government in Yaounde, three hundred kilometers away over very bad roads, for a massive water adduction system using urban technology. The chance that the proposal would be accepted was small. Many hundreds of villageswere competing for the central government's limited resources. But if Ngon should happen to be the lucky winner, the rewards would be great, especially for the members of the Committee of Village Development. The decision was made unanimously to proceed with Plan B. As a result, at least up to the time when my daughter left the country, Ngon still had no water supply.

After the meetings were over, my daughter went back to the village and spoke privately with the villagers, trying to understand why they had made what seemed to her a clearly wrong decision. She found that everybody, including the women who carry the waterpots to and from the spring, was in favor of Plan B. In the end, they almost convinced my daughter that Plan B made sense. After all, as oneof the women said to my daughter, nobody in Ngon ever dies of thirst. The problem of the water supply is not a matter of life and death. The problem is a matter of status. On the one hand, the act of writing an official proposal to the government would enhance the status of the village and of the Committee of Village Development, even if nothing ever came of it. It would open a channel of communication and create contacts between the villagers and the political authorities in Yaounde. In the long run, suchcontacts are more important to the life of the village than a communal bathhouse. On the other hand, the act of making a deal with a backwoods well digger would be unworthy of the dignity of an official Committee of Village Development. If these arguments had not been sufficient, there was an even more cogent reason for rejecting Plan A. The well digger is a Fulani. He belongs to the wrong tribe. The Boulous of Ngon are a settled agricultural people. They have lived from time immemorial in villages and consider themselves civilized. The Fulanis are northerners, nomads, and cowherds. No self-respecting Boulou would want to take orders from a Fulani.

So I leave the villagers of Ngon, on the whole a happy and contented people. They were always friendly and hospitable to my daughter, even when they found her ideas a little strange. I pass on now from the third to the second world.

2. THE SECOND WORLD

To represent the second world I choose the great Soviet astronomical observatory at Zelenchukskaya in the Caucasus Mountains. I visited the observatory in 1977. The six-meter telescope, the largest optical telescope in the world, was then brand-new and just beginning to go into operation. I spent three days and nights on the mountain and enjoyed my stay very much. The astronomers at Zelenchakskaya were as friendly to me as the villagers of Ngon were to my daughter. They talked frankly about the six-meter telescope and its history.

Twenty years earlier a committee of the Soviet Academy had met to discuss with the political authorities the facilities for optical astronomy in the Soviet Union. The six-meter telescope was their Plan B. Plan A was to construct four or five modern observatories of modest size at optically excellent sites in Central Asia. One example of a Plan A observatory already existed at Byurakan in Soviet Armenia. The Armenians are the Fulanis of the Sovie Union. I also visited Byurakan and saw there a two-meter telescope with a Fulani by the name of Markaryan in charge. Markaryen was using his telescope to great effect, taking pictures of the sky with an objective grating and picking out objects that have strong emission in the blue and violet parts of the spectrum. Many of the most interesting objects in the universe were first identified by Markaryan and still carry Markaryan's catalog numbers. Byurakan has been for thirty years in the hands of Fulanii who know how to do important science with limited means.

Unfortunately, there are no other observatories like Byurakar in the Soviet Union. Instead, Plan B prevailed. The committee of academicians decided to build the biggest telescope in the world. Six meters was chosen as the mirror diameter because it had to bc decisively bigger than the five-meter telescope at Palomar. The manufacture of the telescope was entrusted to a heavy industrial outfit in Leningrad which had little previous experience with astronomy. The observatory was under construction for twenty years. When I visited it in 1977, one of the Soviet astronomers remarked that the structure was built out of leftover pieces from dismantled battleships. Another Soviet astronomer told me that this one instrument had set back the progress of optical astronomy in the Soviet Union by twenty years. It had absorbed for twenty years the major part ofthe funds assigned to telescope building, and it was in many ways already obsolete before it began to operate. It deprived a generation of young astronomers of the opportunity to put their skills to use. Now another thirteen years have gone by and the telescope has set back the progress of astronomy in the Soviet Union by thirty-three years.

One of the factors which the committee planning the observatory did not worry about was the Zelenchukskaya weather. I was on the mountain for three nights and did not see the sky. Even at Mount Palomar one may be unlucky and run into a string of cloudy nights. But at Zelenchukskaya the weather is consistently bad for the greater part of each year. The site is far too close to the high Caucasus peaks which are regularly stirring up storms and clouds. The committee probably chose this site because it is easily accessible by rail and road. The sites with good astronomical seeing in Central Asia may have been excluded because they have no roads suitable for the transport ofasupermassive structure. At Zelenchukskaya the roads are good because there is a skiing resort in the same valley. Of course, the snow which makes the area good for skiing also causes problems for the telescope. When I was there, a great mass of accumulated ice had blocked the action of the dome so that the slit could not be opened. Even if the sky had been clear, the telescope would not have been able to see it. I gave a theoretical seminar to the astronomers in a lecture room where the temperature was minus ten Celsius. The situation did not look good for anybody who wanted to do serious work in astronomy.

During my stay at Zelenchukskaya, I looked for clues which might explain how this scientific disaster had happened. I found the essential clue in the visitors' gallery. Some of you may have gone as tourists to visit the 5-meter telescope at Palomar. Palomar has a visitors' gallery, a glass-enclosed area inside the dome where tourists can see the telescope but cannot pollute the air around it with the heat and humidity of their breathing. At Zelenchokskaya they have a visitors' gallery, like the one at Palomar, only about ten times as big. And behind the visitors' gallery at Zelenchukskaya they have a white wall for visitors to write their names on. Instead of a visitors' book they have a wall, and they invited me to write my name on the wall. The wall is huge, about a hundred feet long, and still I had a hard time finding an empty space large enough to write my name on. Every square inch of the wall was tightly packed with names.

When I saw that wall, I understood for the first time what the Zelenchukskaya observatory was for. The government officials who decided to build the observatory twenty years earlier did not care much about astronomy. They did not mind keeping the astronomers waiting for twenty years while the telescope was being built. Even when the telescope was finished, they were not in any hurry to get the dome unstuck so that the astronomers could get to work. For those government officials the things that mattered were the visitors' gallery and the wall. The visitors' gallery and the wall must have been given high priority. They were in full swing for many years before the telescope was ready. For years and years before my visit, busloads of schoolteachers and factory workers and party chairmen were trooping through the visitors' gallery, admiring this latest triumph of Soviet science, and writing their names on the wall.

Plan B gave the political authorities in Moscow what they wanted, a tangible symbol of Soviet greatness. Plan A might have been better for science. Plan A might have saved a whole generation of astronomers from frustration. But with plan A, the political authorities would not have had the satisfaction of building the biggest telescope in the world, and there would have been no hundred-foot wall for the visitors to write their names on.

3. THE FIRST WORLD

My third cautionary tale concems our own world, the so-called first world. The astronomers of the United States have made ahabit of setting up a committee at the beginning of each decade to plan the facilities to be built in the subsequent ten years. The committees are called by the names of their chairmen, all of them distinguished astronomers. The first was the Whitford Committee which made plans for the 1960s. Next came the Greenstein Committee which dealt with the 1970s. I shall talk about the third committee, the Field Committee, which dealt with the 1980s and published its report in 1982. The Field Committee had a number of sensible recommendations for ground-based astronomy which I shall not discuss. I shall talk only about the problems of space-based astronomy, the launching and operation of astronomical telescopes in orbit.

While the Field Committee was meeting from 1978 to 1980, the situation of American space-based astronomy was roughly as follows. We had two active space telescope projects with very different characteristics. We had one Boulou space telescope and one Fulani space telescope. The Boulou telescope was the Hubble Space Telescope, a grand and elaborate instrument which had already been recommended by the Greenstein Committee ten years earlier and was supposed to be launched by the shuttle, if all went well, in 1985. The Fulani telescope was a small and comparatively cheap instrument called the International Ultraviolet Explorer, or the IUE, which had not been recommended by the Greenstein Committee or by any other prestigious committee of experts. I will have more to say about the IUE in chapter 5 [of From Eros to Gaia]. The IUE was launched in January 1978, before the Field Committee started work, and has been from the beginning, like Markaryan's telescope in Armenia, a brilliant scientific success. It is still going strong and still doing excellent science after twelve years in space.

The Field Committee considered two programs of space-based astronomy which I will call Plan A and Plan B. I am here interpreting the committee's discussions in my own way. You won't find any explicit mention of Plan A and Plan B in the committee report. Plan A was a series of Explorer missions following the pattern of the IUE. An Explorer mission means a mission small enough and cheap enough to be paid for out of the NASA space science budget without special exertions. Roughly speaking, each Explorer mission costs about one-fifth of the annual space science budget. If Explorer missions were given the highest priority, it would be possible for NASA to sustain a launch rate of one astronomical Explorer per year in addition to the Explorers concerned with other things such as earth-science and plasma physics. There are many important things for astronomical Explorers to do. If we had one Explorer mission in X-ray astronomy, one in infrared, one in extreme ultraviolet, one in astrometry, and one in radio interferometry, the scientific harvest would be enormous. If Plan A had been adopted, we could have had all of these flying in the 1980s without any stretching ofthe NASA space-science budget.

The Field Committee, however, like thecommittees in Ngon and in Moscow, preferred Plan B. Plan B consisted of a series of space missions known collectively as Great Observatories. The Hubble Space Telescope was the first Great Observatory. After that would come the Gamma-Ray Observatory, also dependent on the shuttle for its launch and scheduled to go up in 1987. Next would be the Advanced X-ray Astrophysics Facility, familiarly known as AXAF. AXAF was the highest-priority item on the Field Committee list of new missions, since the committeeas sumed the first two Great Observatories, the Hubble Telescope and the Gamma-Ray Observatory, to be already in the bag. After AXAF would come a fourth Great Observatory called LDR, or Large Deployable Reflector, a far-infrared telescope with mirror diameter in the ten-meter class. Plan B began with these four Great Observatory missions, plus a number of smaller missions left over from earlier committee reports. To be fair I should mention that Plan B included an Explorer mission called IRAS or Infrared Astronomy Satellite which flew in 1983 and gave us our first comprehensive view of the infrared universe. IRAS was, like the earlier Explorer mission IUE, an international venture and an enormous scientific success.

The main emphasis in the Field Committee report was on the Great Observatories. Each Great Observatory costs as much as five or ten Explorers. Each requires protracted and diffiicult negotiations between NASA and various committees of Congress to obtain the necessary funds. Each requires about a decade to complete its engineering development and construction after its funding has been authorized. And each requires a shuttle launch to put it into orbit. As a consequence of the Challenger disaster of January 1986, the Great Observatories have been delayed by an additional three or four years. The scientific return from the entire Plan B program, apart from IRAS and some ground-based activities which I am not discussing here, has been in no way commensurate with its cost. Just like in Ngon. Just like in Zelenchukskaya.

It is important to understand that the debacle of the Great Observatory program is not simply a consequence of the shuttle accident. The Great Observatories were in deep trouble long before the Challenger crashed. Their troubles were technical as well as political. The Hubble Telescope, the only Great Observatory yet built, had a long history of engineering difficulties, delays, and cost overruns. Even if the shuttle had remained alive and well, none of the missions recommended by the Field Committee and not already recommended by earlier committees could possibly have been launched in the 1980s. The Field Committee report was entitled Astronomy and Astrophysics for the 1980s. The title shows that the members of the committee were deluding themselves. So far as the 1980s were concerned, their program was a mirage.

The fundamental flaw in the Great Observatory program is ecological. The Great Observatories are too big and too slow and too expensive to fit comfortably into the ecology of science. They take so long to fund, to build and to launch that they are unable to keep pace with the rapid growth of science. Scientific discoveries emerge, scientific ideas change, and scientific tools develop, all within a year or two. A Great Observatorywhich takes ten years to build is always in danger of being left behind. The ecology of science needs missions that are small, cheap, and quick enough to respond to new ideas and new questions. This is true, whether or not the shuttle crashes.

That is theend of my third tale. One moral of these tales is clear. The nature of committees is the same, whether it is revealed in an African village assembly or in the academic politics of Moscow and Washington. The same drama is played, whether it is the Committee of Village Development, the Soviet Academy of Sciences, or the Field Committee that takes the leading role. The ascendancy of the committeemen began early in the history of science. One of the decisive steps in their upward progress in the United States occurred in 1906, when the administrators of the newly established Carnegie Institution, at that time the largest source of money for scientific research, announced that funding would be denied for "the amateur, the dilettante and the tyro." In other words, to qualify for funding you had better have a Ph.D., a certificate of academic respectability. Well diggers need not apply.

The game of status seeking, organized around committees, is played in roughly the same fashion in Africa and in America and in theSoviet Union. Perhaps the aptitude for this game is a part of our genetic inheritance, like the aptitude for speech and for music. The game has had profound consequences for science. In science, as in the quest for a village water supply, big projects bring enhanced status; small projects do not. In the competition for status, big projects usually win, whether or not they are scientifically justified. As the committees of academic professionals compete for power and influence, big science becomes more and more preponderant over small science. The large and fashionable squeezes out the small and unfashionable. The space shuttle squeezes out the modest and scientifically more useful expendable launcher. The Great Observatory squeezes out the Explorer. The centralized adductlon system squeezes out the village well. Fortunately, the American academic system is pluralistic and chaotic enough that first-rate small science can still be done in spite of the committees. In odd corners, in out-of-the-way universities, and in obscure industrial laboratories, our Fulanis are still at work.

4. TWO SUCCESS STORIES

I am tempted to say that the moral of these stories is that committees are the root of all evil. Let us abolish committees and see how science will flourish. But life is not so simple. My stories were chosen with a certain bias. I could tell some other stories about committees which did not do so badly. In the ecology of science, as in the ecology of nature, there must be a balance between big and small enterprises. We cannot all be Fulanis. Even committees have a place in the ecology.

To be fair, let me tell next a story in which Plan B turned out to be right. I go back to the Greenstein report of 1972, the predecessor of the Field report. Like other committees, the Greenstein Committee recommended a Plan B in which the highest-priority item was also the biggest. The highest priority was given to the Very Large Array, or VLA, a huge Y-shaped array of radio telescopes to be constructed in the New Mexico desert near Socorro. The scientific purpose of the VLA was to provide pictures of remote and complex radio sources with an angular resolution surpassing the best optical telescopes. The beautiful multicolored VLA pictures of radio galaxies and supernova remnants on the covers of magazines such as Scientific American and Sky and Telescope are sufficient proof that the VLA has been an outstanding success. It is the finest general-purpose radio telescope in the world. It has fulfilled abundantly the Greenstein Committee's expectations. Even more remarkably, in comparison with other large projects, the VLA is cost-effective. After the Greenstein Committee recommended it in 1972, it was built for a total cost of $78 million and finished in 1980, on schedule and within budget. In performance it is comparable with a Great Observatory, but in cost it is comparable with an Explorer.

There are many reasons for the success of the VLA. First of all, it is large but not disproportionately large. It forms part of a worldwide community of instruments, some large and some small, which conveniently share the work of exploring the radio sky. The VLA did not absorb the lion's share of the funds spent on astronomy in the 1970s. It did not squeeze out smaller enterprises. In other words,it found its niche at the top of the food chain in a well-balanced ecology.

Another reason for the VLA's success is that it was built quickly enough so that it was not overtaken by newer technologies. A third reason is that Jesse Greenstein himself was acutely aware of the danger of big projects squeezing out small ones. He is, in his own professional life, a Fulani. He likes to study small, dim, peculiar stars that nobody else is interested in. He made sure that, in spite of the VLA, small-scale science got its fair share of emphasis in the Greenstein report. To achieve this balance between big and small, he had to threaten to quit as committee chairman. I quote now a few sentences from a personal account which he wrote twelve years later:

The VLA is successful. Its story is a useful one for aspiring promoters of further large projects. The issue of balance between individual and national goals is indirectly addressed in the [Greenstein] report. During our final discussions, it caused me intense discomfort. I resigned for a brief time as chairman, since I was uncertain that I could fully support all the recommendations. That survey report is schizoid as published. It says, build large new national instruments, but [in brackets] please do not neglect to support university scientists and their new instruments. The parenthetical phrase may be intellectually correct but it is impotent, with no political or budgetary clout. The individualistic style of my own research was possible at institutions founded to pursue new, unplanned and often changing goals. That system was good. I remain skeptical that it is completely outmoded.

So I leave Jesse Greenstein, musing over the possibly destructive effects of the juggernaut which he helped to set in motion. The moral of this story is, if you have to have a committee to apportion resources between large and small projects, make sure that the chairman is as wise and as sensitive as Jesse Greenstein.

My next story is a more recent one. During the last few years the community of molecular biologists in the United States has been struggling with the question of whether to set up a large project to map and sequence the human genome, the set of 3 billionbase pairs in the genes of a human being. To map means to find out roughly where each of the genes is sitting; to sequence means to find out exactly where each base pair in the whole genome is sitting. Following the example of the astronomers, they appointed a committee. The chairman of the committee was Bruce Alberts, a microbiologist at the University of California at San Francisco. The committee published its report in 1988. The report marked a turning point in the history of biology. It was the first time that biologists had to face the possibility that Big Science might cometo dominate their activities as it has dominated astronomy and physics.

The Alberts Committee, like other committees, had its Plan A and Plan B. Plan A was to continue unchanged so far as possible the existing way of doing things, with mapping and sequencing activities carried on in decentralized fashion by many groups of scientists investigating particular problems of human genetics. In Plan A there would be no centralized big project, and no drive to sequence the 3 billion bases of the human genome in their entirety irrespective of their genetic significance. Plan B would be the opposite. Plan B would establish an industrial-scale facility for sequencing, and would aim to have the whole job done by an army of technicians within a few years. In conjunctionwith the sequencing project there would also be a large centralized mapping project, using the sequence data to identify all known and unknown human genes with precisely known places in the genome. Plan B would require a large new expenditure of public funds, with the usual attendant problems of deciding who should administer the funds and who should receive them.

According to Bruce Alberts, the members of his committee were at the beginning sharply split, with some favoring Plan A and some Plan B. He himself claimed to be neutral, but he is, like Jesse Greenstein, a strong defender of the importance of small science. In his own laboratory he studies with a team of colleagues and students the details of the machinery of DNA replication. He is by temperamentcloser to Plan A than to Plan B. Nevertheless, he observed, during the year that his committee was meeting, that the opinions of the members converged upon a plan that was neither A nor B but a compromise somewhere in between. The compromise plan was recommended unanimously in the committeeÍs report, after Walter Gilbert, the only irreconcilable advocate of Plan B, had resigned. Roughly speaking, the recommended compromise plan is three-quarters A and one-quarter B.

The Alberts Committee recommendations are as follows. First no crash program to sequence the genome. Second, mapping and sequencing activities continue to be conducted by local groups as before, with an informal international division of labor. Third, mapping and sequencing to be driven by theneeds of genetic science and medicine, with nonhuman and human genomes treated alike. Fourth, mapping to have higher priority than sequencing. So far, the recommendations are pure Plan A, but now comes a little of Plan B. Fifth, substantial new money, estimated at $200 million a year for fifteen years, to be spent in support of mapping and sequencing. Sixth, a substantial fraction of this money to be spent on development of new technology for radically cheaper and faster sequencing. Seventh, centralized facilities to be set up for the two services which require them, a data bank of DNA sequences to be collected from all over the world and stored on computers, and a clone bank of actual pieces of DNA that have been mapped or sequenced. The data-bank and theclone-bank should be fully documented and accessible to the world community of scientists.

In my opinion, these recommendations embody considerable wisdom. They are politically and technically feasible. The new money that they require is only 3 percent of the annual National Institutes of Health budget for biology and medical research. Of this3 percent, only a fraction will go into centralized facilities. The new facilities are not on such a scale as to squeeze out the I small teams of scientists who will be doing the bulk of the work in human genetics. In spite of my bias against committees, I have to admit that the Alberts Committee, like the Greenstein Comimittee, made the right choices.

The Alberts Committee is noncommittal about the main question it was originally asked to decide, whether and when the entire human genome should be sequenced. The committee says the complete sequence should not be a primary objective. The complete sequence should be done when, and only when, we have developed the technology to do the job cheaply and quickly. When it can be done cheaply, go ahead and do it. But don't waste large quantities of money and manpower on an objective that is not scientifically essential.

The complete human genome sequence in biology is like the Palomar Sky Survey in astronomy. The Palomar Sky Survey is a complete set of photographs of the northern half of the sky, taken with the 48-inch Schmidt telescope on Mount Palomar during the years 1949 to 1956. It was later extended to the Southern Hemisphere, using a similar Schmidt telescope in Australia. At every major observatory in the world, there is a set of Palomar Sky Survey plates, copied from the original plates at Palomar. The Palomar plates are enormously useful to astronomers. Before you decide to point a telescope at something interesting in the sky, you have a look at the Palomar.plate to see what that piece of the sky looks like. The plates are also used by many astronomers for statistical work, for counting stars and galaxies and clustersand measuring their distributions on the sky. When we have a complete human genome sequence, it will be used in the same way. Every microbiological or medical research laboratory will have a copy of it handy. When you want to study any particular gene, youwill look first at the genome sequence to see what the neighboring DNA looks like. And the sequence as a whole will be a primary tool for statistical studies of human genetics and evolution.

The Palomar Sky Survey was remarkably cheap. The entire project was funded privately by the National Geographic Society, without any government money. It cost altogether about a million dollars. In 1956 you could buy a complete set of Sky Survey plates for about $2,000. The invention of the Schmidt camera reduced the cost of photographing large areas of sky by a factor of a hundred. Before the Schmidt telescope was invented in 1930, there had been an international project with the name Carte du Ciel, which tried to make a complete sky survey with ordinary telescopes. The Carte du Ciel languished because the work was tedious and no end was in sight. After the Schmidt camera came along, a small group of dedicated and hardworking people could finish the job in seven years. The project became so obviously cost-effective that the necessary funds could be raised without much difficulty.

It is likely that the human-genome-sequencing project will have a similar history. At present, the cost of sequencing is about one dollar per base. Since the genome has 3 billion bases, the entire sequence using present-day technology would cost $3 billion. At that price it makes no sense to do it. But one day some clever inventor will find the equivalent of the Schmidt camera. When the cost of sequencing comes down to one cent per base, the whole sequence will cost $30 million, roughly five times the cost of the Palomar Sky Survey in 1990 dollars. Then we will be able to do not just a single human genome but complete sequences of genomes of men and women with a variety of medical histories, not to mention chimpanzees, mice, fruit flies, frogs, and bacteria. In the end, the limit to the sequencing of genomes will probably be set, not by the cost of sequencing, but by our ability to digest and use the vast amount of information that the sequences contain.

The Alberts Committee wisely refrained from recommending a fixed timetable for the mapping and sequencing program. How fast it goes will depend on discoveries and inventions still to be made. Their essential recommendation, for dealing with a situation of immense promise and immense uncertainty, was to stay flexible and avoid premature commitment to rigid programs. This is a recommendation that ought to apply just as well to physics and astronomy as it does to biology. Unfortunately, in the history of committees planning scientific programs, such wisdom is rare.

5. THE SUPERCONDUCTING SUPERCOLLIDER

My final story is the Superconducting Supercollider or SSC. This story is still unfinished. The SSC is a proposed machine for doing high-energy physics. It was recommended to the United States government in 1984 by a committee of famous particle physicists. The committee is called HEPAP, High-Energy Physics Advisory Panel. The SSC was formally approved by President Reagan in 1987. It is a ring-shaped proton accelerator of stupendous size. It will be the biggest accelerator in the world and will reach the highest energy. It will cost about $8 billion and will take about ten years to build, if the remaining financial and technical uncertainties can be overcome.

The SSC is an extreme example of Plan B. The question we have to address is whether SSC is a good Plan B like the Very Large Array or a disastrous Plan B like Zelenchakskaya. Nobody can be sure of the answer to this question. I do not claim to be infallible when I make guesses about thefuture. But the SSC shows all the characteristic symptoms of a bad Plan B. It is bad politically because it is being pushed by economic interests and by considerations of national prestige having little to do with scientific merit. It is bad educationally because it pours money into a project which offers little opportunity for creative involvement of students. It is bad scientifically because the proton-proton collisions which it produces are peculiarly difficult to interpret. It is bad ecologically because it squeezes out other avenues of research which are likely to lead to more cost-effective high-energy accelerators. None of these arguments by itself is conclusive, but together they make a strong case against the SSC. There is a serious risk that the SSC will be as great a setback to particle physics as the Zelenchukskaya Observatory has been to astronomy.

When I discuss these misgivings with my particle physicist friends, some who belong to HEPAP and some who don't, they usually say things like this: "But look, we have no alternative. If we want to see the Higgs boson, or the top quark, or the photino, orany other new particles going beyond the standard model, we have to go to higher energy. It is either the SSC or nothing." This is the same kind of talk you always hear when people are arguing for Plan B. It is either Plan B or nothing. This argument usually prevails because Plan B is one big thing and Plan A is a lot of little things. When your eyes are blinded by the glitter of something big, all thelittle things look like nothing. Fortunately, this argument did not prevail on the Alberts Committee. The biologists on the committee knew that the small items of genome mapping in Plan A add up to more scientific knowledge than one big sequence.

But to answer the physicists who say "SSC or nothing," we must produce a practical alternative to the SSC. We must have a Plan A. Plan A does not mean giving up on high-energy physics. It does not mean that we stop building big accelerators. It does not mean that we lose interest in Higgs bosons and top quarks. My Plan A is rather like the plan recommended by the Alberts Committee. It says, let us put more money into exploring new ideas for building cost-effective accelerators. Let us build several clever accelerators instead of one dumb accelerator. Let us measure the value of an accelerator by its scientific output rather than by its energy input. And meanwhile, while the technology for cheaper and better accelerators is being developed, let us put more money into using effectively the accelerators we already have.

The advocates of the SSC often talk as if the universe were one-dimensional, with energy as the only dimension. Either you have the highest energy or you have nothing. But in fact the world of particle physics is three-dimensional. The three dimensions in a particle physics experiment are energy, accuracy, and rarity. Energy and accuracy have obvious meanings. Energy is determined mainly by the accelerator, accuracy by the detection equipment. Rarity means the fraction of particle collisions that produce the particular process that the experiment is designed to study. To observe events of high rarity, we need an accelerator with high intensity to make a large number of collisions, and we also need a detector with good diagnostics to discriminate rare events from background.

I am not denying that energy is important. Let us by all means build accelerators of higher energy when we can do so cost-effectively. But energy is not the only important variable. If we look back over the history of particle physics for the last forty years, we can identify nine experimental discoveries that were of preeminent scientific importance. My list agrees with the judgments expressed by the Nobel Prize Committee in their awards. By and large, the Nobel Committee has done an excellent job in picking out the contributions that everybody agrees are important.

Each of the big experimental discoveries happens on some frontier between known and unknown territory. If a discovery results from observing things at higher energy than anybody has done before, then I say it is on the energy frontier. If a discovery results from measuring things with higher accuracy than has been done before, then I say it is on the accuracy frontier. If a discovery results from observing events that are rarer than anybody has seen before, then I say it is on the rarity frontier. When you look at the list of nine crucial experiments, you find three experiments on the energy frontier, three on the accuracy frontier, and three on the rarity frontier. The fact that the numbers come out exactly equal is not important. You could choose different criteria and come out with different numbers. The important point is that the numbers of discoveries on the three frontiers are comparable. In some rough sense the three frontiers are equally promising places to look for new laws of nature. This is what I mean when I say that the world of particle physics is three-dimensional and not one-dimensional. Only one-third of the frontier lies in the direction of higher energy.

My Plan A for the future of particle physics is a program giving roughly equal emphasis to the three frontiers. Plan A should be a program of maximum flexibility, encouraging the exploitation of new tools and new discoveries wherever they may occur. To encourage work on the accuracy frontier means continuing to put major effort into new detectors to be used with existing accelerators. To encourage work on the rarity frontier means building some new accelerators which give high intensity of particles with moderate energy.After these needs are taken care of, Plan A will still include big efforts to move ahead on the energy frontier. But the guiding principle should be: more money for experiments and less for construction. Let us find out how to explore the energy frontiercheaply before we get ourselves locked into a huge construction project. Let us follow the good example of the Alberts Committee when they say: "Because the technology required to meet most of the project's goals needs major improvement, the committee specifically recommends against establishing one or a few large sequencing centers at present."

Plan A consists of a mixture of many different programs, looking for opportunities to do great science on all three frontiers. Plan A lacks the grand simplicity andpredictability of the SSC. And that is to my mind the main reason for preferring Plan A. There is no illusion more dangerous than the belief that the progress of science is predictable. If you look for nature's secrets in only one direction, you are likely to miss the most-important secrets, those which you did not have enough imagination to predict.

This essay is reprinted from From Eros to Gaia, copyright © 1992 by Freeman Dyson. Used by permission of the author. Do not reprint without permission.