Nonsense arguments for building a bigger particle collider that I am tired of hearing (The Ultimate Collection)

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I know you’re all sick of hearing me repeat why a larger particle collider is currently not a good investment. Trust me, I am sick of it too. To save myself some effort, I decided to collect the most frequent arguments from particle physicists with my response. You’ve heard it all before, so feel free to ignore.

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.

Superfluid Dark Matter [Video]

I am at home with a cold, and so I finally got around to finish this video on superfluid dark matter which has been sitting on my hard disk for a few months.


This is a sequel to my earlier two videos about Dark Matter and Modified Gravity.

For captions, click CC in the tool bar. Will add German captions in the next days. Now I need a few ibuprofen.

Just Move (I’ve been singing again)

I have spent the last few weekends shouting at a foam mat. It’s nothing personal. Foam and I, we normally get along just fine. It’s just that I was hoping to improve my singing technique. Also, shouting may come in handy on other occasions, you never know.

Alas, my shouting success was limited. It’s hard to project anger at a foam mat. But somewhere along the way I seem to have spontaneously developed a head-voice vibrato, not sure how come. Probably a sign that my head is becoming increasingly hollow.

Besides that, I have a new pre-amplifier which works better than the previous one, but has a markedly different noise pattern that I yet have to get used to. If my voice sounds different, that’s probably why. That, or the hollow head.

(Soundcloud version here.)

Science has a problem. Here is how you can help.

[I have gotten numerous requests by people who want to share Appendix C of my book. The content is copyrighted, of course, but my publisher kindly agreed that I can make it publicly available. You may use this text for non-commercial purposes, so long as you add the copyright disclaimer, see bottom of post.]

Both bottom-up and top-down measures are necessary to improve the current situation. This is an interdisciplinary problem whose solution requires input from the sociology of science, philosophy, psychology, and – most importantly – the practicing scientists themselves. Details differ by research area. One size does not fit all. Here is what you can do to help.

As a scientist:

• Learn about social and cognitive biases: Become aware of what they are and under which circumstances they are likely to occur. Tell your colleagues.
• Prevent social and cognitive biases: If you organize conferences, encourage speakers to not only list motivations but also shortcomings. Don’t forget to discuss “known problems.” Invite researchers from competing programs. If you review papers, make sure open questions are adequately mentioned and discussed. Flag marketing as scientifically inadequate. Don’t discount research just because it’s not presented excitingly enough or because few people work on it.
• Beware the influence of media and social networks: What you read and what your friends talk about affects your interests. Be careful what you let into your head. If you consider a topic for future research, factor in that you might have been influenced by how often you have heard others speak about it positively.
• Build a culture of criticism: Ignoring bad ideas doesn’t make them go away, they will still eat up funding. Read other researchers’ work and make your criticism publicly available. Don’t chide colleagues for criticizing others or think of them as unproductive or aggressive. Killing ideas is a necessary part of science. Think of it as community service.
• Say no: If a policy affects your objectivity, for example because it makes continued funding dependent on the popularity of your research results, point out that it interferes with good scientific conduct and should be amended. If your university praises its productivity by paper counts and you feel that this promotes quantity over quality, say that you disapprove of such statements.

As a higher ed administrator, science policy maker, journal editor, representative of funding body:

• Do your own thing: Don’t export decisions to others. Don’t judge scientists by how many grants they won or how popular their research is – these are judgements by others who themselves relied on others. Make up your own mind, carry responsibility. If you must use measures, create your own. Better still, ask scientists to come up with their own measures.
• Use clear guidelines: If you have to rely on external reviewers, formulate recommendations for how to counteract biases to the extent possible. Reviewers should not base their judgment on the popularity of a research area or the person. If a reviewer’s continued funding depends on the well-being of a certain research area, they have a conflict of interest and should not review papers in their own area. That will be a problem because this conflict of interest is presently everywhere. See next 3 points to alleviate it.
• Make commitments: You have to get over the idea that all science can be done by postdocs on 2-year fellowships. Tenure was institutionalized for a reason and that reason is still valid. If that means fewer people, then so be it. You can either produce loads of papers that nobody will care about 10 years from now, or you can be the seed of ideas that will still be talked about in 1000 years. Take your pick. Short-term funding means short-term thinking.
• Encourage a change of field: Scientists have a natural tendency to stick to what they know already. If the promise of a research area declines, they need a way to get out, otherwise you’ll end up investing money into dying fields. Therefore, offer reeducation support, 1-2 year grants that allow scientists to learn the basics of a new field and to establish contacts. During that period they should not be expected to produce papers or give conference talks.
• Hire full-time reviewers: Create safe positions for scientists specialized in providing objective reviews in certain fields. These reviewers should not themselves work in the field and have no personal incentive to take sides. Try to reach agreements with other institutions on the number of such positions.
• Support the publication of criticism and negative results: Criticism of other people’s work or negative results are presently underappreciated. But these contributions are absolutely essential for the scientific method to work. Find ways to encourage the publication of such communication, for example by dedicated special issues.
• Offer courses on social and cognitive biases: This should be mandatory for anybody who works in academic research. We are part of communities and we have to learn about the associated pitfalls. Sit together with people from the social sciences, psychology, and the philosophy of science, and come up with proposals for lectures on the topic.
• Allow a division of labor by specialization in task: Nobody is good at everything, so don’t expect scientists to be. Some are good reviewers, some are good mentors, some are good leaders, and some are skilled at science communication. Allow them to shine in what they’re good at and make best use of it, but don’t require the person who spends their evenings in student Q&A to also bring in loads of grant money. Offer them specific titles, degrees, or honors.

As a science writer or member of the public, ask questions:

• You’re used to asking about conflicts of interest due to funding from industry. But you should also ask about conflicts of interest due to short-term grants or employment. Does the scientists’ future funding depend on producing the results they just told you about?
• Likewise, you should ask if the scientists’ chance of continuing their research depends on their work being popular among their colleagues. Does their present position offer adequate protection from peer pressure?
• And finally, like you are used to scrutinize statistics you should also ask whether the scientists have taken means to address their cognitive biases. Have they provided a balanced account of pros and cons or have they just advertised their own research?

You will find that for almost all research in the foundations of physics the answer to at least one of these questions is no. This means you can’t trust these scientists’ conclusions. Sad but true.

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Reprinted from Lost In Math by Sabine Hossenfelder. Copyright © 2018. Available from Basic Books, an imprint of Perseus Books, a division of PBG Publishing, LLC, a subsidiary of Hachette Book Group, Inc

Particle physicists continue to spread misinformation about prospects of new collider

Physics Today has published an essay by Gordon Kane about “The collider question.”

Gordon Kane is Professor of Physics at the University of Michigan. He is well known in the field, both for his research and his engagement in science communication. Kane has written several well-received popular science books about particle physics in general, and supersymmetry in particular.

In his new essay for Physics Today, Kane mentions “economic considerations” and the possibility of spin-offs in favor of a larger collider. But these are arguments that could be made about any experiment of similar size.

His key point is that a next larger collider is needed to answer some of the currently open big questions in the foundations of physics:

“For our next colliders the goal is to provide data for a more comprehensive theory, hopefully one that incorporates dark matter, quantum gravity, and neutrino masses and solves the hierarchy problem. But what does that mean in practice?”

He claims that:

“It’s been known since the 1980s that a mathematically consistent quantum theory of gravity has to be formulated in 9 or 10 spatial dimensions.”

This statement is wrong. It is known that string theory requires additional dimensions of space, but physicists do not presently know that string theory is the correct theory for quantum gravity. They also have several other, mathematically consistent, approaches to quantum gravity that do not require additional dimensions, such as asymptotically safe gravity, or loop quantum gravity.

Kane then refers to an earlier article he wrote about his own models for Physics Today and claims:

“They predict or describe the Higgs boson mass. We can now study the masses that new particles have in such models to get guidance for what colliders to build.”

Note the odd phrase “predict or describe the Higgs boson mass.” The story here is that in 2011 Kane and collaborators, a few days before CERN collaborations released first results of the Higgs measurement, published a paper claiming they can predict the correct Higgs-mass. Kane later wrote a Comment about this for Nature Magazine. All particle physicists I ever spoke with about Kane’s prediction suspect it was informed by rumors about the Higgs mass and then, consciously or unconsciously, backward constructed.

In his Physics Today essay, Kane then goes on to write that his models “generically have some observable superpartners with masses between about 1500 GeV and 5000 GeV” and argues that:

“Such theoretical work provides quantitative predictions to help set goals for collider construction, similar to how theorists helped zero in on the mass of the Higgs boson.”

Gordon Kane has made predictions for the appearance of new particles at colliders for 20+ years. Every time an experiment fails to see those new particles, he adjusts the masses so that the theory is still compatible with data. For references, please check out Will Kinney’s recent twitter thread.

Among particle physicists, Kane is somewhat exceptional by his public presence and the boldness of his assertions. But his method of making predictions is typical practice in the field. Indeed, by the current standard in particle physics, his research is of high quality. Kane’s models are well-motivated by beautiful ideas and, together with his collaborators, he has amassed a lot of impressive looking equations, not to mention citations.

This does not change the fact that those predictions are worthless.

Allow me an analogy. Forget for a moment that we are talking about particle physics, and think of climate science. That’s the stuff with global warming and melting ice sheets and so on, I’m sure you’ve heard. Now imagine that those models could predict literally any possible future trend. That would be pretty useless predictions, wouldn’t you agree? It wouldn’t be much of a science, really. It would be pretty ridiculous, indeed.

Well, that’s how predictions for new particles currently work. The methods of theory-development used by particle physicists can predict anything and everything.

You do not have to take my word for it, you only have to look at this paper about “ambulance chasing”. Ambulance chasing is the practice of particle physicists to cook up models to explain statistical fluctuations that they hope will turn out to be real particles. With the currently accepted methods of model-building, they can produce hundreds of explanations within months, regardless of whether the signal was actually real or not.

You do not even need to understand a single word written in those papers to see that one cannot trust predictions made this way.

I don’t want to pick on Kane too much, because he just does what he has learned, and he does an excellent job at this. But Gordon Kane is to particle physics what Amy Cuddy is to psychology: A very public example of scientific methodology gone badly wrong.

Like Cuddy, the blame is not on Kane in particular, the blame is on a community which is not correcting a methodology they all know is not working. The difference is that while psychologists have recognized the problems in their community and have taken steps towards improvement, particle physicists still refuse to acknowledge their field even has a problem.

The methods of theory-development used in particle physics to predict new physics are not proper science. This research must be discontinued. And it should certainly not be used to argue we need a next larger collider.

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Correction, March 18: I have been informed that Physics Today is not the membership magazine of the American Physical Society, it is just that members of the American Physical Society receive the magazine. I therefore rewrote the first sentence.

Particle physicists excited over discovery of nothing in particular

Logo of Moriond meeting.

“Rencontres de Moriond” is one of the most important annual conferences in particle physics. This year’s meeting will start in two days, on March 16th. Usually, experimental collaborations try to have at least preliminary results to present at the conference, so we have an interesting couple of weeks ahead.

The collaboration of the ATLAS experiment at CERN has already released a few results from the searches for “exotic” particles with last year’s run 2 data. So far, they have seen nothing new. More results will likely appear online soon. 

One of the key questions to be addressed by the new data analysis is whether the “lepton flavor anomalies” persist. These anomalies are several small differences between rates of processes that, according to the standard model, should be identical. Separately, each deviation from the standard model has a low statistical significance, not exceeding 3 σ. However, in 2017 a group of particle physicists claimed that the combined significance exceeds 5 σ.

You should take such combined analyses with several grains of salt. Choosing some parts of the data while disregarding others makes the conclusion unreliable. This does not mean the result is wrong, just that it’s impossible to know if it is a real effect or a statistical fluctuation. Really this question can only be resolved with more data. CMS, another one of the LHC experiments, recently tested a specific explanation for the anomaly but found nothing.

Meanwhile it must have dawned on particle physicists that the non-discovery of fundamentally new particles besides the Higgs is a problem for their field, and especially for the prospects of financing that bigger collider which they want. For two decades they told the public that the LHC would help answering some “big questions,” for example by finding dark matter or supersymmetric particles, illustrated well by this LHC outreach website:

Screenshot of the LHC Outreach website.

However, the predictions for new particles besides the Higgs were all wrong. And now, rather than owning up to their mistakes, particle physicists want you to think it’s exciting they have found neither dark matter, nor extra dimensions, nor supersymmetry, nor anything else that is not in the standard model. In a recent online article at Scientific American, James Beacham is quoted saying:

“We’re right on the cusp of a revolution but we don’t really know where that revolution is going to be coming from. It’s so exciting and enticing. I would argue there’s never been a better time to be a particle physicist.”

The particle physicist Jon Butterworth says likewise:

“It’s more exciting and more uncertain now than I think it’s ever been in my career.”

And Nima Arkani-Hamed, in an interview with the CERN Courier begins his answer to the question “How do you view the status of particle physics?” with:

“There has never been a better time to be a physicist.”

The logic here seems to be this: First, mass-produce empty predictions to raise the impression that a costly experiment will answer some big questions. Then, if the experiment fails to answer those questions, proclaim how exciting it is that your predictions were wrong. Finally, explain that you need money for a larger experiment to answer those big questions.

The most remarkable thing about this is that they actually seem to think this will work.

Needless to say, if the analysis of the recent data reveals a signal of new effects, then the next collider will be built for sure. If nothing new shows up, then particle physicists can either continue to excitedly deny anything went wrong, or realize they have to act against hype and group-think in their community. The next weeks will be interesting.

Motte and Bailey, Particle Physics Style

“Motte and bailey” is a rhetorical maneuver in which someone switches between an argument that does not support their conclusion but is easy to defend (the “motte”), and an argument that supports their conclusion but is hard to defend (the “bailey”). The purpose of this switch is to trick the listener into believing that the easy-to-defend argument suffices to support the conclusion.

This rhetorical trick is omnipresent in arguments that particle physicists currently make for building the next larger collider.

There are good arguments to build a larger collider, but those don’t justify the investment. These arguments are measuring the properties of known particles to higher precision and keeping particle physicists occupied. Also, we could just look and see if we find something new. That’s the motte.

Then there is an argument which would justify the investment, but this is not based on sound reasoning. This argument is that a next larger collider would lead to progress in the foundations of physics, for example by finding new symmetries or solving the riddle of dark matter. This argument is indefensible because there is no reason to think the next larger collider would help answering those questions. That’s the bailey.

This maneuver is particularly amusing if you both have people who make the indefensible argument and others who insist no one makes it. In a recent interview with the CERN courier, for example, Nima Arkani-Hamed says:

“Nobody who is making the case for future colliders is invoking, as a driving motivation, supersymmetry, extra dimensions…”

While his colleague, Lisa Randall, has defended the investment into the next larger collider by arguing:

“New dimensions or underlying structures might exist, but we won’t know unless we explore.”

I don’t think that particle physicists are consciously aware of what they are doing. Really, I get the impression they just throw around whatever arguments come to their mind and hope the other side doesn’t have a response. Most unfortunately, this tactic often works, just because there are few people competent enough to understand particle physicists’ arguments and also willing to point out when they go wrong.

For this reason I want to give you an explicit example for how motte and bailey is employed by particle physicists to make their case. I do this in the hope that it will help others notice when they encounter this flawed argument.

The example I will use is a recent interview I did for a podcast with the Guardian. The narrator is Ian Sample. Also on the show is particle physicist Brian Foster. I don’t personally know Foster and never spoke with him before. You can listen to the whole thing here, but I have transcribed the relevant parts below. (Please let me know in case I misheard something.)

At around 10:30 min the following exchange takes place.

Ian: “Are there particular things that physicists would like to look for, actual sort-of targets like the Higgs, that could be named like the Higgs?”

Brian: “The Higgs is really, I think, at the moment the thing that we are particularly interested in because it is the new particle on the block. And we know very little about it so far. And that will give us hopefully clues as to where to look for new phenomena beyond the standard model. Because the thing is that we know there must be physics beyond the standard model. If for no other reason than, as you mention, there’s very strong evidence that there is dark matter in the universe and that dark matter must be made of particles of some sort we have no candidate for those particles at the moment.”

I then explain that this argument does not work because there is no reason to think the next larger collider would find dark matter particles, that, in fact, we are not even sure dark matter is made of particles.

After some more talk about the various proposals for new colliders that are currently on the table, the discussion returns to the question what justifies the investment. At about 24:06 you can hear:

Ian: “Sabine, you’ve had a fair bit of flak for some of your criticisms for the FCC, haven’t you, from within the community?”

Sabine: “Sure, true, but I did expect it. Fact is, we have no reason to think that a next larger particle collider will actually tell us anything new about the fundamental laws of nature. There’s certainly some constants that you can always measure better, you can always say, well, I want to measure more precisely what the Higgs is doing, or how that particle decays, and so on and so forth. But if you want to make progress in our understanding of the foundations of physics that’s just not currently a promising thing to invest in. And I don’t think that’s so terribly controversial, but a lot of particle physicists clearly did not like me saying this publicly.”

Brian: “I beg to differ, I think it is very controversial, and I think it’s wrong, as I’ve tried to say several times. I mean the way in which you can make progress in particle physics is by making these precision measurements. You know very well that quantum mechanics is such that if you can make very high precision measurements that can tell you a lot of things about much higher energies than what you can reach in the laboratory. So that’s the purpose of doing very high precision physics at the LHC, it’s not like stamp collecting. You are trying to make measurements which will be sufficiently precise that they will give you a very strong indication of where there will be new physics at high energies.”

(Only tangentially relevant, but note that I was talking about the foundations of physics, whereas Brian’s reply is about progress in particle physics in particular.)

Sabine: “I totally agree with that. The more precisely you measure, the more sensitive you are to the high energy contributions. But still there is no good reason right now to think that there is anything to find, is what I’m saying.”

Brian: “But that’s not true. I mean, it’s quite clear, as you said yourself, that the standard model is incomplete. Therefore, if we can measure the absolutely outstanding particle in the standard model, the Higgs boson, which is completely unique, to very high precision, then the chances are very strong that we will find some indication for what this physics beyond the standard model is.”

Sabine: “So exactly what physics beyond the standard model are you referring to there?

Brian: “I have no idea. That’s why I want to do the measurement.”

I then explain why there is no reason to think that the next larger collider will find evidence of new physical effects. I do this by pointing out that the only reliable indications we have for new physics merely tell us something new has to appear at latest at energies that are still about a billion times higher than what even the next larger collider could reach.

At this point Brian stops claiming the chances are “very strong” that a bigger machine would find something new, and switches to the just-look-argument:

Brian: “Look, it’s a grave mistake to be too strongly lead by theoretical models [...]”

The just-look-argument is of course well and fine. But, as I have pointed out many times before, the same just-look-argument can be made for any other new experiment in the foundations of physics. It therefore does not explain why a larger particle collider in particular is a good investment. Indeed, the opposite is the case: There are less costly experiments for which we have good reasons, such as measuring more precisely the properties of dark matter or probing the weak field regime of quantum gravity.

When I debunk the just-look-argument, a lot of particle physicists then bring up the no-zero-sum-argument. I just did another podcast a few days ago where the no-zero-sum-argument played a big role and if that appears online, I’ll comment on that in more detail.

The real tragedy is that there is absolutely no learning curve in this exchange. Doesn’t matter how often I point out that particle physicists’ arguments don’t hold water, they’ll still repeat them.

(Completely irrelevant aside: This is the first time I have heard a recording made in my basement studio next to other recordings. I am pleased to note all the effort I put into getting good sound quality paid off.)

Inflation: Status Update

Model of Inflation.
img src: umich.edu

The universe hasn’t always been this way. That the cosmos as a whole evolves, rather than being eternally unchanging, is without doubt one of the most remarkable scientific insights of the past century. It follows from Einstein’s theory of general relativity: Einstein’s theory tells us that the universe must expand. As a consequence, in the early universe matter must have been compressed to high density.

But if you follow the equations back in time, general relativity eventually stops working. Therefore, no one presently knows how the universe began. Indeed, we may never know.

Since the days of Einstein, physicists have made much progress detailing the history of the universe. But the deeper they try to peer into our past, the more difficult their task becomes.

This difficulty arises partly because new data are harder and harder to come by. The dense matter in the early universe blocked light, so we cannot use light to look back to any time earlier than the formation of the cosmic microwave background. For even earlier times, we can make indirect inferences, or hope for new messengers, like gravitational waves or neutrinos. This is technologically and mathematically challenging, but these are challenges that can be overcome, at least in principle. (Says the theorist.)

The more serious difficulty is conceptual. When studying the universe as whole, physicists face the limits of the scientific method: The further back in time they look, the simpler their explanations become. At some point, then, there will be nothing left to simplify, and so there will be no way to improve their explanations. The question isn’t whether this will happen, the question is when it will happen.

The miserable status of today’s theories for the early universe makes me wonder whether it has already happened. Cosmologists have hundreds of theories, and many of those theories come in several variants. It’s not quite as bad as in particle physics, but the situation is similar in that cosmologists, too, produce loads of ill-motivated models for no reason other than that they can get them published. (And they insist this is good scientific practice. Don’t get me started.)

The currently most popular theory for the early universe is called “inflation”. According to inflation, the universe once underwent a phase in which volumes of space increased exponentially in time. This rapid expansion then stopped in an event called “reheating,” at which the particles of the standard model were produced. After this, particle physics continues the familiar way.

Inflation was originally invented to solve several finetuning problems. (I wrote about this previously, and don’t want to repeat it all over again, so if you are not familiar with the story, please check out this earlier post.) Yall know that I think finetuning arguments are a waste of time, so naturally I think these motivations for inflations are no good. However, just because the original reason for the idea of inflation doesn’t make sense doesn’t mean the theory is wrong.

Ever since the results of the Planck in 2013 it hasn’t looked good for inflation. After the results appeared, Anna Ijjas, Paul Steinhardt, and Avi Loeb argued in a series of papers that the models of inflation which are compatible with the data themselves require finetuning, and therefore bring back the problem they were meant to solve. They popularized their argument in a 2017 article in Scientific American, provocatively titled “Pop Goes the Universe.”

The current models of inflation work not simply by assuming that the universe did undergo a phase of exponential inflation, but they moreover introduce a new field – the “inflaton” – that supposedly caused this rapid expansion. For this to work, it is not sufficient to just postulate the existence of this field, the field also must have a suitable potential. This potential is basically a function (of the field) and typically requires several parameters to be specified.

Most of the papers published on inflation are then exercises in relating this inflaton potential to today’s cosmological observables, such as the properties of the cosmic microwave background.

Now, in the past week two long papers about all those inflationary models appeared on the arXiv:

Cosmic Inflation: Trick or Treat?
By Jerome Martin
arXiv:1902.05286 [astro-ph.CO]

and

Inflation after Planck: Judgement Day
By Debika Chowdhury, Jerome Martin, Christophe Ringeval, Vincent Vennin
arXiv:1902.03951 [astro-ph.CO]

The first paper, by Jerome Martin alone, is a general overview of the idea of inflation. It is well-written and a good introduction, but if you are familiar with the topic, nothing new to see here.

The second paper is more technical. It is a thorough re-analysis of the issue of finetuning in inflationary models and a response to the earlier papers by Ijjas, Steinhardt, and Loeb. The main claim of the new paper is that the argument by Ijjas et al, that inflation is “in trouble,” is wrong because it confuses two different types of models, the “plateau models” and the “hilltop models” (referring to different types of the inflaton potential).

According to the new analysis, the models most favored by the data are the plateau models, which do not suffer from finetuning problems, whereas the hilltop models do (in general) suffer from finetuning but are not favored by the data anyway. Hence, they conclude, inflation is doing just fine.

The rest of the paper analyses different aspects of finetuning in inflation (such as quantum contributions to the potential), and discusses further problems with inflation, such as the trans-planckian problem and the measurement problem (as pertaining to cosmological perturbations). It is a very balanced assessment of the situation.

The paper uses standard methods of analysis (Bayesian statistics), but I find this type of model-evaluation generally inconclusive. The problem with such analyses is that they do not take into account the prior probability for the models themselves but only for the initial values and the parameters of the model. Therefore, the results tend to favor models which shove unlikeliness from the initial condition into the model (eg the type of function for the potential).

This is most obvious when it comes to the so-called “curvature problem,” or the question why the universe today is spatially almost flat. You can get this outcome without inflation, but it requires you to start with an exponentially small value of the curvature already (curvature density, to be precise). If you only look at the initial conditions, then that strongly favors inflation.

But of course inflation works by postulating an exponential suppression that comes from the dynamical law. And not only this, it furthermore introduces a field which is strictly speaking unnecessary to get the exponential expansion. I therefore do not buy into the conclusion that inflation is the better explanation. On the very contrary, it adds unnecessary structure.

This is not to say that I think inflation is a bad idea. It’s just that I think cosmologists are focusing on the wrong aspects of the model. Finetuning arguments will forever remain ambiguous because they eventually depend on unjustifiable assumptions. What’s the probability for getting any particular inflaton potential to begin with? Well, if you use the most common measure on the space of all possible function, then all so-far considered potentials have probability zero. This type of reasoning just does not lead anywhere. So why waste time talking about finetuning?

Instead, let us talk about those predictions whose explanatory value does not depend on finetuning arguments, of which I suspect (but do not know) that ET-correlations in the CMB power spectrum are an example. Since finetuning debates will remain unsolvable, it would be more fruitful to focus on those benefits of inflation that can be quantified unambiguously.

In any case, I am sure the new paper will make many cosmologists happy, and encourage them to invent many more models for inflation. Sigh.

Merchants of Hype

Once upon a time, the task of scientists was to understand nature. “Merchants of Light,” Francis Bacon called them. They were a community of knowledge-seekers who subjected hypotheses to experimental test, using what we now simply call “the scientific method.” Understanding nature, so the idea, would both satisfy human curiosity and better our lives.

Today, the task of scientists is no longer to understand nature. Instead, their task is to uphold an illusion of progress by wrapping incremental advances in false promise. Merchants they still are, all right. But now their job is not to bring enlightenment; it is to bring excitement.

Nowhere is this more obvious than with big science initiatives. Quantum computing, personalized medicine, artificial intelligence, simulated brains, mega-scale particle colliders, and everything nano and neuro: While all those fields have a hard scientific core that justifies some investment, the big bulk is empty headlines. Most of the money goes into producing papers whose only purpose is to create an appearance of relevance.

Sooner or later, those research-bubbles become unsustainable and burst. But with the current organization of research, more people brings more money brings more people. And so, the moment one bubble bursts, the next one is on the rise already.

The hype-cycle is self-sustaining: Scientists oversell the promise of their research and get funding. Higher education institutions take their share and deliver press releases to the media. The media, since there’s money to make, produce headlines about breakthrough insights. Politicians are pleased about the impact, talk about international competitiveness, and keep the money flowing.

Trouble is, the supposed breakthroughs rarely lead to tangible progress. Where are our quantum computers? Where are our custom cancer cures? Where are the nano-bots? And why do we still not know what dark matter is made of?

Most scientists are well aware their research floats on empty promise, but keep their mouths shut. I know this not just from my personal experience. I know this because it has been vividly, yet painfully, documented in a series of anonymous interviews with British and Australian scientists about their experience writing grant proposals. These interviews, conducted by Jennifer Chubb and Richard Watermeyer (published in Studies in Higher Education), made me weep:

“I will write my proposals which will have in the middle of them all this work, yeah but on the fringes will tell some untruths about what it might do because that’s the only way it’s going to get funded and you know I’ve got a job to do, and that’s the way I’ve got to do it. It’s a shame isn’t it?”
(UK, Professor)

“If you can find me a single academic who hasn’t had to bullshit or bluff or lie or embellish in order to get grants, then I will find you an academic who is in trouble with his Head of Department. If you don’t play the game, you don’t do well by your university. So anyone that’s so ethical that they won’t bend the rules in order to play the game is going to be in trouble, which is deplorable.”
(Australia, Professor)

“We’ll just find some way of disguising it, no we’ll come out of it alright, we always bloody do, it’s not that, it’s the moral tension it places people under.”
(UK, Professor)

“They’re just playing games – I mean, I think it’s a whole load of nonsense, you’re looking for short term impact and reward so you’re playing a game... it’s over inflated stuff.”
(Australia, Professor)

“Then I’ve got this bit that’s tacked on... That might be sexy enough to get funded but I don’t believe in my heart that there’s any correlation whatsoever... There’s a risk that you end up tacking bits on for fear of the agenda and expectations when it’s not really where your heart is and so the project probably won’t be as strong.”
(Australia, Professor)

In other interviews, the researchers referred to their proposals as “virtually meaningless,” “made up stories” or “charades.” They felt sorry for their own situation. And then justified their behavior by the need to get funding.

Worse, the above quotes only document the tip of the iceberg. That’s because the people who survive in the current system are the ones most likely to be okay with the situation. This may be because they genuinely believe their field is as promising as they make it sound, or because they manage to excuse their behavior to themselves. Either way, the present selection criteria in science favor skilled salesmanship over objectivity. Need I say that this is not a good way to understand nature?

The tragedy is not that this situation sucks, though, of course, it does. The tragedy is that it’s an obvious problem and yet no one does anything about it. If scientists can increase their chances to get funding by exaggeration, they will exaggerate. If they can increase their chances to get funding by being nice to their peers, they will be nice to their peers. If they can increase their chances to get funding by publishing on popular topics, they will publish on popular topics. You don’t have to be a genius to figure that out.

Tenure was supposed to remedy scientists’ conflict of interest between truth-seeking and economic survival. But tenure is now a rarity. Even the lucky ones who have it must continue to play nice, both to please their institution and keep the funding flowing. And honesty has become self-destructive. If you draw attention to shortcomings, if you debunk hype, if you question the promise of your own research area, you will be expelled from the community. A recent commenter on this blog summed it up like this:

“at least when I was in [high energy physics], it was taken for granted that anyone in academic [high energy physics] who was not a booster for more spending, especially bigger colliders, was a traitor to the field.”

If you doubt this, think about the following. I have laid out clearly why I do not think a bigger particle collider is currently a good investment. No one who understands the scientific and technological situation seriously disagrees with my argument; they merely disagree with the conclusions. This is fine with me. This is not the problem. I don’t expect everyone to agree with me.

But I also don’t expect everyone to disagree with me, and neither should you. So here is the puzzle: Why can you not find any expert, besides me, willing to publicly voice criticism on particle physics? Hint: It’s not because there is nothing to criticize.

And if you figured this one out, maybe you will understand why I say I cannot trust scientists any more. It’s a problem. It’s a problem in dire need of a solution.

This rant, was, for once, not brought on by a particle physicist, but by someone who works in quantum computing. Someone who complained to me that scientists are overselling the potential of their research, especially when it comes to large investments. Someone distraught, frustrated, disillusioned, and most of all, unsure what to do.

I understand that many of you cannot break the ranks without putting your jobs at risk. I do not – and will not – expect you to sacrifice a career you worked hard for; no one would be helped by this. But I want to remind you that you didn’t become a scientist just to shut up and advocate.

Check your Biases

[slide 8 of this presentation]

Physics World recently interviewed the current director of CERN, Fabiola Gianotti. When asked how particle physicists address group-think, Gianotti explains instead why some research avenues require large communities.

You would think that sufficiently much has been written about cognitive biases and logical fallacies that even particle physicists took note, but at least the ones I deal with have no clue. If I ask them what measures they take to avoid cognitive biases when evaluating the promise of a research direction, they will either mention techniques to prevent biased data-analysis (different thing entirely), or they will deny that they even have biases (thereby documenting the very problem whose existence they deny).

Here is a response I got from a particle physicist when I pointed out that Gianotti did not answer the question about group think:

(This person then launched an ad-hominem attack at me and eventually deleted their comment. In the hope that this deletion documents some sliver of self-insight, I decided to remove identifying information.)

Here is another particle physicist commenting on the same topic, demonstrating just how much these scientists overrate their rationality:

It is beyond me why scientists are still not required to have basic training in the sociology of science, cognitive biases, and decision making in groups. Such knowledge is necessary to properly evaluate information. Scientists cannot correctly judge the promise of research directions unless they are aware how their opinions are influenced by the groups they are part of.

It would be easy enough to set up online courses for this. If I had the funding, I would do it. Alas, I don’t. The only thing I can do, therefore, is to ask everyone – and especially those in leadership positions – to please take the problem seriously. Scientists are human. Leaving cognitive biases unchecked results in inefficient allocations of research funding, not to mention that it wastes time.

In all brevity, here are the basics.

What is a social bias, what is a cognitive bias?

A cognitive bias is thinking shortcut that has developed through evolution. It can be beneficial in some situations, but in other situations it can result in incorrect judgement. A cognitive bias is similar to an optical illusion. Look at this example:

Example of optical illusion. A and B have the same color.
Click here if you don’t believe it. [Image source: Wikipedia]

The pixels in the squares A and B have the exact same color. However, to most people, square B looks lighter than A. That’s because there is a shadow over square B, so your brain factors in that the original color should have been lighter.

The conclusion that B is lighter, therefore, makes perfect sense in a naturally occurring situation. When asked to judge the color on your screen, however, you are likely to give a wrong answer if you are not aware of how your brain works.

Likewise, a cognitive bias happens if your brain factors in information that may be relevant in some situations but can lead to wrong results in others. A social bias, more specifically, is a type of cognitive bias that comes from the interaction with other people.

It is important to keep in mind that cognitive biases are not a sign of lacking intelligence. Everyone has cognitive biases and that’s nothing to be ashamed of. But if your job is to objectively evaluate information, you should be aware that the results of your evaluation are skewed by the way your brain functions.

Scientists, therefore, need to take measures to prevent cognitive biases the same way that they take measures to prevent biases in data analysis. The brain is yet another apparatus. Understanding how it operates is necessary to arrive at correct conclusions.

There are dozens of cognitive biases. I here merely list the ones that I think are most important for science:

• Communal Reinforcement
  More commonly known as “group think,” communal reinforcement happens if members of a community constantly reassure each other that what they are doing is the right thing. It is typically accompanied by devaluing or ignoring outside opinions. You will often see it come along with arguments from popularity. Communal reinforcement is the major reason bad methodologies can become accepted practice in research communities.
  
  
• Availability Cascades
  What we hear of repeatedly sounds more interesting, and we talk more about what is more interesting, which makes it sound even more interesting. This does make a lot of sense if you want to find out what important things are happening in your village. It does not make sense, however, if your job is, say, to decide what’s the most promising experiment to make progress in the foundations of physics. Availability cascades are a driving force in scientific fashion trends and can lead to over-inflated research bubbles with little promise.
  
  
• Post-purchase Rationalization
  This is the tendency to tell ourselves and others that we have not made stupid decision in the past, like, say, pouring billions of dollars in to entirely fruitless research avenues. It is a big obstacle to learning from failure. This bias is amplified by our desire to avoid cognitive dissonance, that is any threat to our self-image as a rationally thinking individual. Post-purchase rationalization is why no experiment in the history of science has ever been a bad investment.
  
  
• Irrational Escalation
  Also known as the “sunk cost fallacy” or “throwing good money after bad.” Irrational Escalation is the argument that you cannot give up now because you have invested so much already. This is one of the main reasons why research agendas survive well beyond the point at which they stopped making sense, see supersymmetry, string theory, or searches for dark matter particles that become heavier and more weakly interacting every time they are not found.
  
  
• Motivated Reasoning
  More collectively known as “wishful thinking,” motivated reasoning is the human tendency to give pep talks and then actually believe the rosy picture we painted ourselves. While usually well-intended, motivated reasoning can result in overly optimistic expectations and an insistence to hold onto irrational dreams. Surely particle physicists are just about to discover some new particle, the next round of experiments will find that dark matter candidate, etc.

There are practical measures you can implement to alleviate these biases, both in your institution and in your personal work-life. In the appendix of my book I list a few. But the most important step is that you acknowledge the existence of these biases whenever you evaluate information and at least try to correct your assessment.

The more people have told you that a crappy scientific method is okay, the more likely you are to believe it is okay. Keep that in mind next time a BSM phenomenologist tells you it is totally normal when a scientific discipline makes wrong predictions for 40 years.

The easiest way to see that particle physics has a big problem with cognitive biases is that members of this community deny they even have biases and refuse to do anything about it.

The topic of cognitive biases has been extensively covered elsewhere, and I see no use in repeating what others have said better. Google will give you all the information you need. Some good starting points are:

• The Cognitive Bias Cheat Sheet, Buster Benson 
• 20 cognitive biases that screw up your decisions, Business Insider  
• How to Reduce Bias In Decision-Making, USC Marshall Critical Thinking Initiative