1. The “Just look” argument.
This argument goes: “We don’t know that we will find something new, but we have to look!” or “We cannot afford to not try.” Sometimes this argument is delivered with poetic attitude, like: “Probing the unknown is the spirit of science” and similar slogans that would do well on motivational posters.
Science is exploratory and to make progress we should study what has not been studied before, true. But any new experiment in the foundations of physics does that. You can probe new regimes not only be reaching higher energies, but also by reaching higher resolution, better precision, bigger systems, lower temperatures, less noise, more data, and so on.
No one is saying we should stop explorative research in the foundations of physics. But since resources are limited, we should invest in experiments that bring the biggest benefit for the projected cost. This means the higher the expenses for an experiment, the better the reasons for building it should be. And since a bigger particle collider is presently the most expensive proposal on the table, particle physicists should have the best reasons.
“Just look” certainly does not deliver any such reason. We can look elsewhere for lower cost and more promise, for example by studying the dark ages or heavy quantum oscillators. (See also point 18.)
2. The “No Zero Sum” argument.
“It’s not a zero sum game,” they will say. This point is usually raised by particle physicists to claim that if they do not get money for a larger particle collider, then this does not imply a similar amount of money will go to some other area in the foundations of physics.
This argument is a badly veiled attempt to get me to stop criticizing them. It does nothing to explain why a particle collider is a good investment.
3. Everyone gets to do their experiment!
This usually comes up right after the No-Zero-Sum-argument. When I point out that we have to decide what is the best investment into progress in the foundations of physics, particle physicists claim that everyone’s proposal will get funded.
This is just untrue.
Take the Square Kilometer Array as an example. Its full plan is lacking about $1 billion in funding and the scientific mission is therefore seriously compromised. The FAIR project in Germany likewise had to slim down their aspirations because one of their planned detectors could not be accommodated in the budget. The James Webb Space telescope just narrowly escaped a funding limitation that would have threatened its potential. And that leaves aside those communities which do not have sufficient funding to even formulate proposals for large-scale experiments. (See also point 19.)
Decisions have to be made. Every “yes” to something implies a “no” to something else. I suspect particle physicists do not want to discuss the benefit of their research compared to that of other parts of the foundations of physics because they know they would not come out ahead. But that is exactly the conversation we need to have.
4. Remember the Superconducting Super Collider!
Yes, the Superconducting Super Collider (SSC). I remember. The SSC was planned in the United States in the 1980s. It would have reached energies somewhat exceeding that of the Large Hadron Collider, and somewhat below that of the now planned Future Circular Collider.
Whatever happened to the SSC? What happened is that the estimated cost ballooned from $5.3 billion in 1987 to $10 billion in 1993, and when US congress finally refused to eat up the bill, particle physicists collectively blamed Phillip Anderson. Anderson is a Nobel Prize winning condensed matter physicist who testified before the US congress in opposition of the project, pointing out that society doesn’t stand much to benefit from a big collider.
While Anderson’s testimony certainly did not help, particle physicists clearly use him as a scapegoat. Anderson-blaming has become a collective myth in their community. But historians largely agree the main reasons for the cancellation were: (a) the crudely wrong cost estimate, (b) the end of the cold war, (c) the lack of international financial contributions, and (d) the failure of particle physicists to explain why their mega-collider was worth building. Voss and Koshland, in a 1993 Editorial for Science, summed the latter point up as follows:
“That particle physics asks questions about the fundamental structure of matter does not give it any greater claim on taxpayer dollars than solid-state physics or molecular biology. Proponents of any project must justify the costs in relation to the scientific and social return. The scientific community needs to debate vigorously the best use of resources, and not just within specialized subdisciplines. There is a limited research budget and, although zero-sum arguments are tricky, researchers need to set their own priorities or others will do it for them.”Remember that?
5. It is not a waste of money
This usually refers to this attempted estimate to demonstrate that the LHC has a positive return on investment. That may be true (I don’t trust this estimate), but just because the LHC does not have a negative return on investment does not mean it’s a good investment. For this you would have to demonstrate it would be difficult to invest the money in a better way. Are you sure you cannot think of a better way to invest $20 billion to benefit mankind?
6. The “Money is wasted elsewhere too” argument.
The typical example I hear is the US military budget, but people have brought up pretty much anything else they don’t approve of, be that energy subsidies, MP salaries, or – as Lisa Randall recently did – the US government shutdown.
This argument simply demonstrates moral corruption: The ones making it want permission to waste money because waste of money has happened before. But the existence of stupidity does not justify more stupidity. Besides that, no one in the history of science funding ever got funding for complaining they don’t like how their government spends taxes.
The most interesting aspect of this argument is that particle physicists make it, even make it in public, though it means they basically admit their collider is a waste of money.
7. But particle physicists will leave if we don’t build this collider.
Too bad. Seriously, who cares? This is a profession almost exclusively funded by taxes. We don’t pay particle physicists just so they are not unemployed. We pay them because we hope they will generate knowledge that benefits society, if not now, then some time in the future. Please provide any reason that continuing to pay them is a good use of tax money. And if you can’t deliver a reason, I full well think we can let them go, thank you.
8. But we have unsolved problems in the foundations of physics.
This argument usually refers to the hierarchy problem, dark matter, dark energy, the baryon asymmetry, quantum gravity, and/or the nature of neutrino masses.
The hierarchy problem is not a problem, it is an aesthetic misgiving. For the other problems, there is no reason to think a larger collider would help solving them.
I have explained this extensively elsewhere and don’t want to go into the question what problems make promising research directions here. If you want more details, read eg this or this or my book.
9. So-and-so many billions is only such-and-such a tiny amount per person per day.
I have no idea what this is supposed to show. You can do the same exercise with literally any other expense. Did you know that for as little a tenth of a Cent per year per person I could pay my grad student?
10. Tim Berners-Lee invented the WWW while employed at CERN.
By the same logic we should build patent offices to develop new theories of gravitation.
11. It may lead to spin-offs.
The example they often bring up is contributions to WiFi technology that originated in some astrophysicists’ attempt to detect primordial black holes.
In response, allow me to rephrase the spin-off-argument: Physicists sometimes don’t waste all money invested into foundational research because they accidentally come across something that’s actually useful. That wasn’t what you meant? Well, but that’s what this argument says.
If these spin-offs are what you are really after, then you should invest more into data analysis or technology R&D, or at least try to find out which research environments are likely to benefit spin-offs. (It is presently unclear how relevant serendipity is to scientific progress.) Even in the best case this may be an argument for basic research in general, but not for building a particle collider in particular.
12. A big particle collider would benefit many tech industries and scientific networks.
Same with any other big investment into experimental science. It is not a good argument for a particle collider in particular.
13. It will be great for education, too!
If you want to invest into education, why dig a tunnel along with it?
14. Knowledge about particle physics will get lost if we do not continue.
We have scientific publications to avoid that. If particle physicists worry this may not work, they should learn to write comprehensible papers. Besides, it’s not like particle physicists would have no place to work if we do not build the next mega-collider. There are more than a hundred particle accelerators in the world; the LHC is merely the largest one. Also note that the LHC is not the only experiment at CERN. So, even if we do not build a larger collider, CERN would not just close down.
15. Highly energetic particle collisions are the cleanest way to measure the physics of short distances.
I tend to agree. This is what originally sparked my interest in high energy particle physics. But there is currently no reason to think that the next breakthroughs wait on shorter distances. Times change. The year is 2019, not 1999.
16. Lord Kelvin also said that physics was over and he was wrong
Yeah, except that I am the one saying we could do better things with $20 billion than measuring the next digits of some constants.
17. Particle accelerators are good for other things.
The typical example is that beams of ions can treat certain types of cancer better than the more common radiation therapies. That’s great of course, and I am all in favor of further developing this technology to enable the treatment of more patients, but this is an entirely different research avenue than building a larger collider.
18. You do not know what else we should do.
Sure I do. I wrote a whole book on this: In the foundations of physics, we should focus on those areas where we have inconsistencies, either between experiment and theory, or internal inconsistencies in the theories. Examining such inconsistencies is what has historically led to breakthroughs.
We currently have such situations in the following areas:
(a) Astrophysical and cosmological observations attributed to dark matter. These are discrepancies between theory and data which should be studied closer, until we have pinned down the theory. Some people have mistakenly claimed I am advocating more direct detection experiments for certain types of dark matter particles. This is not so. I am saying we need better observations of the already known discrepancies. Better sky coverage, better resolution, better stats. If we have a good idea what dark matter is, we can think of building a collider to test it, if that turns out to be useful.
(b) Quantum Gravity. The lack of a theory for quantized gravity is an internal theoretical inconsistency. We know it requires solution. A lot of physicists are not interested in experimentally testing this because they think it is not possible. I have previously explained here and here why that is wrong.
(c) The foundations of quantum mechanics: The measurement postulate is inconsistent with reductionism. There is basically no phenomenological or experimental exploration of this.
Needless to say, I think my argument for how to break the current impasse is a good one, but I do not really expect everyone to just agree with it. I am primarily putting this forward because it’s the kind of discussion we should have: We have not made progress in the foundations of physics for 40 years. What can we do about it? At least I have an argument. Particle physicists do not.
19. But you do not have any other worked-out proposals
The proposal for the FCC was worked out by a study group over 5 years, supported by 11 million Euro. Needless to say, I cannot, as a single person and in a few weeks of time, produce comparable proposals for large scale experiments. Expecting me to do so is unreasonable.
20. But it will do all these things
Particle physicists like to point towards their 716 pages report that summarizes what they could do with the FCC. But, look, no one doubts that you can do something with $20 billion. The question is whether what you can do is worth the investment. The report does not address this point at all.