The need for precision, in turn, redoubles the need for that other great Greek tradition, open discussion of ideas and ruthless separation of meaningful things from meaningless ones. Precision alone does not guarantee good law. Financing practices in the Age of Emergence have the side effect of diluting content, engendering the famous joke that the Physical Review is now so voluminous that stacking up successive issues would generate a surface traveling faster than the speed of light - although without violating relativity because the Physical Review contains no information. The problems, which is not restricted to physics, occurs because large experimental laboratories cannot get the continued funding they need without defending their work from criticism, which they typically do by forming self-refereeing monopolies that define certain ideas and bodies of thought to be important, whether they actually are or not… From A Different Universe, by Lauglin, page 215-216
Currently the future of particle physics is completely uncertain. So far, there were no surprising findings at the LHC and no one knows for sure what the best next move is. Would another huge collider, even larger than the LHC, finally bring us the much needed experimental information that help us to figure out the correct theory beyond the standard model? Or would the money be better invested in small projects?
A great answer to this question was already given in 1988 by Freeman Dyson in his essay “Six Cautionary Tales for Scientists”
In this essay Dyson compares 6 situations where people had to decide between a Plan A = several small projects vs. a Plan B = one huge project. His main conclusion is that in most situations “Plan A” is the better option.
One relevant example of his is when “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 billion base pairs in the genes of a human being.” They had the option to “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 conjunction with 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.”
The other option would be 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.”
He then argues that Plan A is the much better option: “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.” Moreover, he concludes that it is clever “to stay flexible and avoid premature commitment to rigid programs. […] Unfortunately, in the history of committees planning scientific programs, such wisdom is rare.”
Instead of investing a large junk of the available budget into one big project, he argues, it makes more sense to give the same money to smaller projects. These smaller projects will help to develop the needed technology further and drive the costs for experiments down. After some years it will be probably possible to get the same results for millions instead of billions. In addition, there is much more flexibility and more possibilities for surprising findings.
His arguments against Plan B’s are even more convincing and relevant for the question whether a new huge collider should be built, when he talks about the SSC.
“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 Zelenchukskaya. […] I do not claim to be infallible when I make guesses about the future. 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, or any 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 the little things look like nothing. […] 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. […]
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 frontier cheaply 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 and predictability 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.“
“We are already at the point where experiments are becoming impossible for technological reasons and unthinkable for social and political reasons. An accelerator bigger than the supercollider would be a vast technical challenge, and even if physicists are willing to try it, the likelihood of society paying the bills seems faint.”
from The End of Physics by Lindley
To quote from it:
“A 100 TeV proton-proton collider could produce conclusive answers to various open questions surrounding the Higgs boson and, in addition, solve some of the most tantalizing puzzles related to the matter-antimatter asym- metry, to dark matter and to dark energy . ”
This is clearly a misleading statement to advertise a new collider. A 100 TeV collider will most certainly not answer conclusively problems surrounding the Higgs, and will not solve the matter-antimatter asymmetry problem, the dark matter problem or the dark energy problem. Of course, the authors write “could”. However, because they use it as an argument in favor of the new collider, it is clear that they imply that the chances are reasonably high. However, if you talk privately to most physicists the probability they would give to the scenario that a 100 TeV would help with any of the questions listed above, is closer to $0.000001 \%$ than to anything that would justify a new collider.
These kind of statements are made by a few prominent physicists and repeated over and over.
The authors above reference Arkani-Hamed to back their claims up, who is a good example for such a prominent figure who likes to promote his own agenda over and over again. He spent the last decades inventing new methods to calculate scattering amplitudes. While these are certainly interesting from a purely theoretical point of view, without a new collider there is little need for new massive scattering amplitude calculations and hence for his new techniques.