Thursday, October 22, 2020

Particle Physicists Continue To Make Empty Promises

[This is a transcript of the video embedded below]

Hello and welcome back to my YouTube channel. Today I want to tell you how particle physicists are wasting your money. I know that’s not nice, but at the end of this video I think you will understand why I say what I say.

What ticked me off this time was a comment published in Nature Physics, by CERN Director-General Fabiola Gianotti and Gian Giudice, who is Head of CERN's Theory Department. It’s called a comment, but what it really is is an advertisement. It’s a sales pitch for their next larger collider for which they need, well, a few dozen billion Euro. We don’t know exactly because they are not telling us how expensive it would be to actually run the thing. When it comes to the question what the new mega collider could do for science, they explain:
“A good example of a guaranteed result is dark matter. A proton collider operating at energies around 100 TeV [that’s the energy of the planned larger collider] will conclusively probe the existence of weakly interacting dark-matter particles of thermal origin. This will lead either to a sensational discovery or to an experimental exclusion that will profoundly influence both particle physics and astrophysics.”
Let me unwrap this for you. The claim that dark matter is a guaranteed result, followed by weasel words about weakly interacting and thermal origin, is the physics equivalent of claiming “We will develop a new drug with the guaranteed result of curing cancer” followed by weasel words to explain, well, actually it will cure a type of cancer that exists only theoretically and has never been observed in reality. That’s how “guaranteed” this supposed dark matter result is. They guarantee to rule out some very specific hypotheses for dark matter that we have no reason to think are correct in the first place. What is going on here?

What’s going on is that particle physicists have a hard time understanding that when Popper went on about how important it is that a scientific hypothesis is falsifiable, he did not mean that a hypothesis is scientific just because it is falsifiable. There are lots of falsifiable hypotheses that are clearly unscientific.

For example, YouTube will have a global blackout tomorrow at noon central time. That’s totally falsifiable. If you give me 20 billion dollars, I can guarantee that I can test this hypothesis. Of course it’s not worth the money. Why? Because my hypothesis may be falsifiable, but it’s unscientific because it’s just guesswork. I have no reason whatsoever to think that my blackout prediction is correct.

The same is the case with particle physicists’ hypotheses for dark matter that you are “guaranteed” to rule out with that expensive big collider. Particle physicists literally have thousands of theories for dark matter, some thousandths of which have already been ruled out. Can they guarantee that a next larger collider can rule out some more? Yes. What is the guaranteed knowledge we will gain from this? Well, the same as the gain that we have gotten so far from ruling out their dark matter hypotheses, which is that we still have no idea what dark matter is. We don’t even know it is a particle to begin with.

Let us look again at that quote, they write:
“This will lead either to a sensational discovery or to an experimental exclusion that will profoundly influence both particle physics and astrophysics.”
No. The most likely outcome will be that particle physicists and astrophysicsts will swap their current “theories” for new “theories” according to which the supposed particles are heavier than expected. Then they will claim that we need yet another bigger collider to find them. What makes me think this will happen? Am I just bitter or cynical, as particle physicists accuse me? No, I am just looking at what they have done in the past.

For example, here’s an oldie but goldie, a quote from a piece written by string theorists David Gross and Edward Witten for the Wall street journal
“There is a high probability that supersymmetry, if it plays the role physicists suspect, will be confirmed in the next decade.”
They wrote this in 1996. Well, clearly that didn’t pan out.

And because it’s so much fun, I want to read you a few more quotes. But they are a little bit more technical, so I have to give you some background first.

When particle physicists say “electroweak scale” or “TeV scale” they mean energies that can be tested at the Large Hadron Collider. When they say “naturalness” they refer to a certain type of mathematical beauty that they think a theory should fulfil.

You see, particle physicists think it is a great problem that theories which have been experimentally confirmed are not as beautiful as particle physicists think nature should be. They have therefore invented a lot of particles that you can add to the supposedly ugly theories to remedy the lack of beauty. If this sounds like a completely non-scientific method, that’s because it is. There is no reason this method should work, and it does as a matter of fact not work. But they have done this for decades and still have not learned that it does not work.

Having said that, here is a quote from Giudice and Rattazzi in 1998. That’s the same Guidice who is one of the authors of the new nature commentary that I mentioned in the beginning. In 1998 he wrote:
“The naturalness (or hierarchy) problem, is considered to be the most serious theoretical argument against the validity of the Standard Model (SM) of elementary particle interactions beyond the TeV energy scale. In this respect, it can be viewed as the ultimate motivation for pushing the experimental research to higher energies.”
Higher energies, at that time, were the energies that have now been tested at the Large Hadron Collider. The supposed naturalness problem was the reason they thought the LHC should see new fundamental particles besides the Higgs. This has not happened. We now know that those arguments were wrong.

In 2004, Fabiola Gianotti, that’s the other author of the new Nature Physics comment, wrote:
“[Naturalness] arguments open the door to new and more fundamental physics. There are today several candidate scenarios for physics beyond the Standard Model, including Supersymmetry (SUSY), Technicolour and theories with Extra-dimensions. All of them predict new particles in the TeV region, as needed to stabilize the Higgs mass. We note that there is no other scale in particle physics today as compelling as the TeV scale, which strongly motivates a machine like the LHC able to explore directly and in detail this energy range.”
So, she claimed in 2004 that the LHC would see new particles besides the Higgs. Whatever happened to this prediction? Did they ever tell us what they learned from being wrong? Not to my knowledge.

These people were certainly not the only ones who repeated this story. Here is for example a quote from the particle physicist Michael Dine, who wrote in 2007:
“The Large Hadron Collider will either make a spectacular discovery or rule out supersymmetry entirely.”
Well, you know what, it hasn’t done either.

I could go on for quite some while quoting particle physicists who made wrong predictions and now pretend they didn’t, but it’s rather repetitive. I have collected the references here. Let us instead talk about what this means.

All these predictions from particle physicists were wrong. There is no shame in being wrong. Being wrong is essential for science. But what is shameful is that none of these people ever told us what they learned from being wrong. They did not revise their methods for making predictions for new particles. They still use the same methods that have not worked for decades. Neither did they do anything about the evident group think in their community. But they still want more money.

The tragedy is I actually like most of these particle physicists. They are smart and enthusiastic about science and for the most part they’re really nice people.

But look, they refuse to learn from evidence. And someone has to point it out: The evidence clearly says their methods are not working. Their methods have led to thousands of wrong predictions. Scientists should learn from failure. Particle physicists refuse to learn.

Particle physicists, of course, are entirely ignoring my criticism and instead call me “anti-science”. Let that sink in for a moment. They call me “anti-science” because I say we should think about where to best invest science funding, and if you do a risk-benefit assessment it is clear that building a bigger collider is not currently a good investment. It is both high risk and low benefit. We would be better off if we'd instead invest in the foundations of quantum mechanics and astroparticle physics. They call me “anti-science” because I ask scientists to think. You can’t make up this shit.

Frankly, the way that particle physicists behave makes me feel embarrassed I ever had anything to do with their field.


  1. Sabine, which potentially more productive experiments could be performed, using the same amount of money as requested for the new collider? It's not a sarcastic question, I would simply like to know.

  2. I am surprised you did not mention CP violations. The origin of this is completely unknown. We have a funny situation where a meson that has right spin can decay and emit an electron aligned with the spin, and similarly if it is left spin it also emits the electron in the direction of the spin. This is a parity violation. Then if we consider the anti-meson spinning right it emits along the direction of the spin, so there is charge violation. Then for the left spinning meson we also get the emission of an electron along the spin, which violates both C and P, or CP. This breaking of C and P and CP symmetry is not known according to the Higgs theory. Without going into detail on this there is the sphaleron theory which is one putative reason for this. I will not of course say I think this is correct, but it is possible. The sphaleron is around 10 TeV and would require 100 TeV energy to reach statistically favorable threshold energy of production.

    My sense is that constructing a 100 TeV based on current accelerator technology is a big part of the problem. If it were possible to get an order of magnitude more E field applied to a particle and also ways of increasing magnetic quadrupole steering magnetic fields we might not have to upscale so dramatically. I should think this would be a much higher priority in the HEP community than what I see.

    When it comes to extremely high energy physics, such as near the Planck scale, I think those secrets may light in sensitive detection of gravitational waves. Quantum hair or the horizon atmospheres of black holes may generate gravitons by mechanisms similar to string theory. The spacetime just before collision is approximately AdS_4 and physics there may be found in nonreversal of the metric with BMS symmetry.

    1. Why would I mention CP violations? CP is violated, so what?

    2. Why is it violated? It seems to be some type of symmetry breaking.

    3. Well,..., there might be some process involved. The sphaleron mechanism is proposed to be in this 100TeV range. That or some other system may be in play.

    4. Lawrence,

      The 100 TeV bound you quote remains is uncertain insofar the production rates of sphaleron transitions is concerned. Many open questions remain, see e.g.

    5. After observing CP violation, perhaps it is more reasonable to conclude that CP symmetry does not exist in our universe than that it results from symmetry breaking by an unknown mechanism. Not that searching for such a mechanism would necessarily be a fools errand...rather, it would arguably be unwise to invest billions investigating a process that has no more concrete reason to exist other than "it would be really nice."

    6. (Please disregard the word "remains" in the first sentence of my reply above; it is a typo).

    7. B-L symmetry is conserved in an instanton. The degree to which B or L changes is a measure of the tunneling barrier. This is not entirely known and the theory is an instanton/soliton or nonperturbative QFT physics and is thus not easily studied with standard techniquies. The extent to which they were abundant in the early universe is an open question. If in the trans-EW physics they are sufficiently abundant then baryon and lepton conservation are only a low energy limit. The magnitude of the tunneling barrier iwht the open question, and the usual estimate is around 10TeV. If the production rate is lower, this means B and L conservation hold at higher energy.

      This might be studied with a Hitchen's Higgs bundle construction (A, φ). I presume this has been done by some researchers. This could of course start with U(2) = SU(2)×U(1) and work up to higher gauge theory groups. There is a question on the interplay between QCD color charge and weak isospin.

      C, P and CP violation has a sense of being due to a symmetry breaking mechanism. This of course could be wrong, but that would be very odd I think. I agree with Sabine that naturalness is not a proof of a theory, but it is motivating.

      Investing in the next collider is a tough call, and to be honest I think more effort should be made to develop non-standard ways of accelerating particles. After all, laser photons can do the same, and because they have much shorter wavelengths than EM fields in cavities they have much higher energy density. It HEP is to have any experimental future with controlled laboratory experiments it can only if we develop ways of being able to put an LHC energy machine within an area non larger than a sports arena.

    8. Lawrence,

      What you say is generally true, but it is not the whole story. Uncertainties in predictions of sphaleron rates are likely to grow far worse upon considering all the “beyond-the-Standard-Model” (BSM) scenarios conjectured to show up above the low TeV scale. Composite Higgs, Technicolor, preons, leptoquarks, dark photons, high-scale SUSY, Randall-Sundrum gravitons, extra-dimensions and so on, are a handful of representative examples along this line.

    9. To be honest the biggest difficulty I do see with sphaleron dynamics at the 10-100 TeV is this is sufficiently low energy so that B-L symmetry and its transformation of baryons to anti-leptons etc should be apparent. In fact I would think a form of proton decay would ensue. Since this is an energy far below the GUT scale this might be readily apparent.

      Most of the BSM theories you mention I suspect are wrong. I think SUSY might hold, but I think it is a Planck or near Planck scale physics process. The SUSY MSSM and low mass SUSY pair physics is not looking at all right. I would also suspect if the scale for any of these physical processes is shoved to near the Planck scale, then I suspect similarly sphaleron physics is also. If so then the next 100TeV collider will register nothing.

    10. I am also utterly unconvinced about the BSM scenarios listed in my previous reply.

      Just to be clear, my only point was to show how uncertain and problematic the whole sphaleron business is when it comes to unveiling the mechanism of CP violation at 100 TeV.

  3. Can anyone play? I offer my equally plausible (I flatter myself) Theory Of Everything (With Artful Allusion To Beneficial Climate Change Side Benefits) Funding Submission Blues:

    Well I woke up this morning
    I got this T of E
    Which the margin of this blog is too narrow
    To contain, unfortunately.
    Move over, Einstein
    You ain’t got nothing on me.

    Well, my theory makes predictions
    As a theory should do:
    Step one, fill a kettle,
    Make it boil is step two.
    Shield your lab against neutrinos
    And the steam will turn blue.

    Blue steam gobbles carbon
    Though it may appear strange
    It will be the salvation
    Of all the endange-
    -Ered creatures and species
    It will stop climate change.

    Well I got a kettle
    Need a whole lot of lead.
    Should I transmute the cosmos
    Or import a sufficient quantity from some convenient corner of the multiverse instead?
    These are the questions
    That rattle round in my head.

    Gonna cost you gazillions -
    Drop all other schemes:
    The AI and qubits
    The colliders and beams
    (And put me in a lifestyle
    Beyond your wildest dreams).

  4. Dear Sabine,

    I think your link to the Nature Physics comment in wrong: it takes me to a paper titled "The advantages of metalenses over diffractive lenses". Did you mean to link to ?

    Best regards,
    Bence Kodaj

    1. Hi Bence,

      Thanks for pointing out, I have fixed this.

  5. Thanks for the shout-out to astroparticle approaches. For some reason, astro-funding bodies (NASA, ESA, JAXA) have always been on the other side of the coin than HEP-funders. Missions have to have explicit science objectives that flow down into concrete requirements on the observatory. The idea of funding something that could find something, but might just put limits on it, doesn't get much traction. A recent exception would be Fermi/GLAST -- but that was jointly funded by NASA and DOE. This approach, however, can be almost as problematic as only going for the "we need to get bigger/higher energy/better" and then we'll find something. Sometimes, you do need to just explore. I'd love to see a funding agency that tried to avoid both Scylla and Charybdis...

  6. That you've been accused of being anti-science hits me particularly hard because I've read your book "Lost In Math." The only place that accusation can fly is inside a tent that really does stink!

  7. The comment article reads rather like an election leaflet, complete with promises ("profoundly influence", "significantly advance") and teasers("boost technological developments") while at the same time covering the authors backsides ("the more difficult it becomes to predict", "it is difficult to anticipate"). There's the, now mandatory, nod to the environmental lobby and finally the plea that we "boldly go where no one has gone before" (more mundanely "The urge to seek answers ... is part of what defines us as humans").
    To sweeten the pill the cost is said to be $30billion over 50 years. Just $600 million a year, less than the current budget, that has to appeal to the politicians and money men...
    The argument for and against a new collider has been and will almost certainly continue to be debated ad nauseam. This article adds little to the debate, those for will remain for, those against against. One can only surmise that the authors are hoping it will be picked up and reported in the popular press as part of an overall publicity strategy. It is, as you say, advertising.

  8. This comment has been removed by the author.

  9. Sabine,

    Very nice! I happened to watch this video on our main TV while my spouse Carol was in the room. She noticed my reactions, and at the end she asked "Do you agree with everything she said?"

    To which I replied "Absolutely, every word of it!"

    Funding games are funding games. At every size scale, the universal rule of funding games is that the folks who are the most clever with words, and the most accustomed to getting boatloads of money for their cleverness, also do not like being called out on it. The very trickiness in the wording in the examples you gave is the best indicator of whether such folks are sincerely dedicated to defending the scientific method, or just trying to make sure their funding doesn't dry up.

  10. Very food article, well written and motivated, even an ignorant like me could more or less understand. And agree.

  11. What about another video on "What is Supersymmetry?" ?
    I don't think a bigger accelerator is likely to produce supersymmetric particles, but supersymmetry is a fertile theoretical idea (also outside particle physics!) that is certainly NOT discredited by some over-optimistic people having made wild claims.

    1. Curious forms of supersymmetry are known in low energy, say MeV energy level, nuclear physics and the SUSY potential plays a role in condensed matter physics. I suspect its high energy physics role is with quantum gravity and holography.

      The minimal supersymmetric standard model (MSSM) is not right. At this stage I would be astounded if the LHC began to find signatures of that. Gordon Kane is singing the blues these days, for his whole career was devoted to this. The STOP, supersymmetric top, quark is just nowhere to be found and the charged Higgs sector of MSSM is absent. It also cannot be much more massive.

  12. There is nothing wrong with being wrong. There is nothing wrong with seeking more money to chase down ideas. What is wrong is to coercively fund projects with low chances of paying off as opposed to other projects that have higher chances of paying off.

    Instead of going on about how x band of scientists is doing it wrong (in this case particle physicists), advocating for those who are doing it right is a superior approach and deserving of more air time.

    Let the people devoted to failed methods seek voluntary donations from their true believers. Science funded from all of our taxes needs to have a better payoff.

    1. In case this was intended to be a stab at me, I have been advocating for those who deserve more support for 15 years.

  13. Everyone who say that extra dimension can generate predictions of physical phenomena should be called "anti-science". Space cannot affect anything - it's only the way to describe.

    For example the curvature of space in GR doesn't tell that gravity is physical mechanism by space geometry. No, it tells that we have got curved spacetime as description. It can reveal that basically the attraction of gravity is not due to any signal (at speed c) from "gravitating matter".

    And dimensions; you can add them easily: scalar property can be described by extra dimension or temporal-spatial curvature can be replaced with arbitary amount of dimensions (but it's not often quite smart).

    And other way: you can reduce dimensions e.g. to 1+1 with new regulations of curvature and interactions getting still the same predictions.

    We must rather consentrate on local (or semilocal :) physical structures i.e. on energy tensor currents.

    1. What you say only has traction with quantum gravitation. As a classical theory of gravitation general relativity very much has spacetime as the field. In that sense we can say FAPP that spacetime curvature determines geodesic, or better put geodesic separation, motion.

  14. "No. The most likely outcome will be that particle physicists and astrophysicsts will swap their current “theories” for new “theories” according to which the supposed particles are heavier than expected."

    That comment is exactly spot-on and can't be emphasized enough. I recall my own disbelief when I heard researchers at the LHC say exactly this after the second run when the collider was operating at optimal energies. They didn't see what their SUSY theory predicted, fine, but to then casually suggest, oh, maybe these particles exist at higher energies, seems like moving the goalpost. Speaking as a former science researcher, this is clearly more wishful thinking than sound scientific methodology.

    From my view, I'm not saying SUSY is a failed theory, but it seems well down the road to failure. I'm not sure spending EUR 30B-50B is worth confirming such failure when there are more worthwhile avenues to explore; much as Sabine has listed out.

  15. You mention risk? What are the risks of building the new equipment?

    1. The risk I am referring to is the risk that it won't teach us anything new.

  16. If they it gets built and they still don't make any new significant discoveries, I have little doubt they will then argue why it then needs to be upgraded to even higher energies.

    The sad part is, it doesn't matter if you’re a highly intelligent, highly educated, in a discipline that demands logical rational thought or not, it is human behavior to convince ourselves that what we feel is still somehow always grounded in rational thought. Our only hope to change this is to recognize and police ourselves as individuals, trying to point it out when demonstrated in others is almost always unproductive.

  17. Dear Sabine,
    There are many valid points in your post. True that the argument that dark matter or supersymmetric particles are just at the next higher energy will not work all the time. So may be it should not be used that often. But there are other points of view also. When SSC was cancelled by U.S. congress after prominent condensed matter theorists vehemently argued against SSC, the saved money did not go to condensed matter or NIH etc. It just disappeared in the federal pot of trillions of dollars, perhaps in military's budget. The saved money was not used to remove poverty or health of poor people either. Then there is some truth in the old technological spin off argument and training of future physicists and engineers. Society does advance because of these. There is no doubt that boost in microelectronics, medical imaging technology due to high energy, nuclear physics, space research and astronomy.
    So at best it is a complicated economics issue. There is no clear cut answer.
    Finally, one can argue that theorists cannot be expected to know everything in advance like astrologers!! Otherwise why do experimental research at all if they can predict everything 100 percent correct?

  18. bee

    would the discover of Protophobic Fifth Force x17 arXiv:1604.07411 [hep-ph]change the proton collider operating at energies around 100 TeV debate ?

    1. no, that's a low-energy phenomenon which you'd better study with other experiments

    2. okay btw what do you think of this -x17

    3. i think there are better things to think about

  19. I am not a physicist, but I do have common sense that appears to be absent in the work of theoretical physicists. I find Sabine a breath of fresh air with her work exposing the "Lost in Math" problem in theoretical physics, as well as the problems with most of the other imaginary and un-physical, theories foisted on the public. I do have colleagues who are physicists who spoke frankly about problems with physics and in the end, it seemed to boil down to the “Lost in Math” issue, and the issue of money. So many physicists really have nothing but have become experts at writing research proposals that profess "we are on the cusp of a big discovery” knowing all the while they probably have NOTHING, but are in big need for their income to continue to flow.

    Additionally, I find it strange that they claim to "reproduce" in colliders the conditions of the early universe at the "beginning", yet I do not think it is possible for them to reproduce on earth the conditions at the beginning, this non-science guy asks, because the conditions on earth do not replicate the conditions at the beginning, for example we have gravity and I do not think there was much in the way of gravity at the beginning as it seems that none of the stuff out there had assembled together yet. So, physicists wanting to make a name for themselves collide particles together at ultra-high speeds, disintegrating them, breaking them all apart and the parts that are left are claimed to be great discoveries in physics. Yet none of their discoveries appear to occur in nature without the help of colliders. What we have is smoke and mirrors, where theoretical "physicists" insure their next grant (money) by asserting claims of major discoveries. In reality I think I might have a better understanding of physics than do most theoretical physicists, as I have never been bogged down in math for the sake of math, yet I have spent my entire life living in nature, observing nature, working with the earth, and although I might name only a couple of Newton's laws, I might have a better understanding of nature and the physical world than theoretical physicists lost in math, who create un-physical mathematical models, and didn’t get outside and observe nature enough.

    I realize that I may have put myself out there to be abused verbally (in writing) but it truly does not take a rocket scientist (pun intended) to observe the public being scammed by some of those in power in the physics community who get funding for big projects with false claims. The end results of all this nonsense being that physics is stalled with little going on and few real discoveries happening.

  20. Hi Sabine,

    I do not remember a community or its leaders agreeing that "we are wrong, this is useless, we have to change our way". (Except maybe by the end of middle age about angels' sex theories.) Why would a scientists community do better? Of course some individual see it like you do - many thanks for writing it.

    You claim that the foundations are stalled, but what is it in the foundations that may be changed? Could you for instance list a set of axioms (or principles) and maybe possible consequences if anyone is wrong? Or maybe just give me a reference.


    1. akidbelle,

      A good example is the community of psychologists. They have noticed and acknowledged their methods are not working and they have taken steps to do something about it. See eg this interview.

      I can't parse your second paragraph, sorry. What may be changed? Axioms for what?

    2. Sabine,

      thanks for the interview. In the second paragraph, for instance in GR gravity is interpreted as a curvature of space-time (that is what I learnt long ago). In QM the wave equations give a density of probability - again interpretation. What would it change to assume different interpretations?

      I understand QFT uses a punctual particle, in string theory a Planck scale string that vibrates. What would it change to assume nothing is there? If there is actually nothing there (say no little thing floating in its wave) what difference does it make? How does that shake the foundations?

      Those examples are certainly poor, I just hope you better understand my question.


    3. It doesn't matter how you interpret math for the outcome of a calculation. Interpretations are just mental aids. One may work better one some, another better for others. But the science remains the same.

    4. Sabine,

      Thanks. Obviously there is only math in your answer. I understand interpreting means I cannot know at all what the real stuff is - not even what it looks like, in the worst case only a tiny bit of what it does. Pretty nice way to be lost and stuck. No?


      PS: Note that I am not trying to be aggressive nor even to criticize, but to better understand the situation (after reading your book).

    5. I have no idea what you want. The reason my book is called "Lost in Math" is that physicists are not taking math seriously enough, not because I want them to "interpret" mathematics.

  21. don't we already (supposedly) have evidence for physics beyond standard model through discovery of non-zero neutrino mass? someone should also ask why we need next generation collider if we already have evidence for Physics beyond standard model

  22. Sabine,

    isn't the same criticism also valid for quantum gravity? There were many promises of measurable effects, but nothing was ever found.

    1. Not sure what you mean. Have there been people who claimed they made predictions for "quantum gravitational" effects which were later not found? Yes. Craig Hogan and Lee Smolin spring to mind. What was wrong with those predictions? Same thing that's wrong with the predictions by particle physicists: They invented models pretty much for the purpose of being testable, models that didn't solve any problem.

      You could say that's equally bad as in particle physics and I would agree for what the theory development is concerned. On the financial side, the loss is a few millions, while in particle physics we are talking a few hundred billions, roughly estimated.

      This is why I have been preaching that history teaches us promising theoretical predictions were based on theories that solved an inconsistency. I am not saying "work on quantum gravity because quantum gravity is good". I am saying "solve an inconsistency regardless of which". It just happens to be the case that there isn't any inconsistency within reach of a next larger collider.

  23. Hi Sabine,

    It feels unfair to judge the entire particle physics community by the people promoting freaky BSM (beyond the Standard Model) scenarios.
    It is certainly the problem of this community that the bizarre BSM scenarios get viral in media and are promoted by the physicists themselves as an ultimate truth.
    However, there are large communities in the LHC experiments who do perform precision measurements of the Standard Model parameters and do not take seriously any long-shot theories, being well aware of all the issues you point out.

    Take alone flavor physics: they do amazing job in the recent years, with dozens of new hadrons discovered each year, and dozens of precision SM measurements performed. (Some of them do constrain BSM scenarios much better than the direct searches!)
    The discoveries of new hadronic states, especially tetraquarks and pentaquarks, start the era of hadron chemistry (study of the non-trivial compounds built of quarks and gluons). There are groups of people in the big LHC experiments who did SUSY searches for their entire life, but now move to flavor physics because it looks much more promising at the moment. I am not mentioning the so-called "flavor anomalies" because there are always some fluctuations which will most likely go away with more data or with more robust SM predictions.
    But it's somewhat unfair that the main focus is shifted towards people searching for freaky things, rather than to the scientists who do well their job and bring the fundamental knowledge about the Standard Model particles. And the same stands for theorists: there are hundreds of people working hard on improving the precision of Standard Model computations, who don't take seriously fancy BSM models.
    Believe me or not, but there's plenty of things to do in particle physics, especially flavor and Higgs sectors, even if the SM is the ultimate truth and there's no "new physics".

    It would be fair to consider these arguments when talking about prospects of particle physics. It is also fair to ask what do these physicists think of future collider ideas (there are many opinions). The shiny side of the LHC is that it allows for multi-tasking and friendly accommodates the QCD and flavor physicists together with the people searching for whatever they want. Will a new collider offer such a possibility? That is the key question to me.
    Just to say that reasoning like "particle physicists are doing useless searches for most-likely-inexistent things" do apply to only a part of the community, and should not be generalized. In the era of post-truth over-generalized statements can easily make harm to the concept of fundamental research as such.


    1. Hi Vitaliy,

      If the rest of particle physicists doesn't speak up and instead allows their spokespeople to propagate nonsense, they are equally guilty. Giudice and Gianotti aren't anyone. They're the leading people of the world's leading particle physics institution.

      Of course all the people who work on not "freaky" things have a reason to allow this to happen. Because without the big claims about new and exciting things, no one would fund their research, and they all know that.

  24. bee,

    on the topic of spending $30 billion on 100tev collider

    since qg phenomena and Observational tests of qg is your expertise can you comment

    Observational tests of the self-dual spacetime in loop quantum gravity

    Authors: Tao Zhu, Anzhong Wang arXiv:2008.08704

    "The self-dual spacetime was derived from the mini-superspace approach, based on the polymerization quantization procedure in loop quantum gravity (LQG). Its deviation from the Schwarzschild spacetime is characterized by the polymeric function P, purely due to the geometric quantum effects from LQG. In this paper, we consider the observational constraints imposed on P by using the solar system experiments and observations. For this purpose, we calculate in detail the effects of P on astronomical observations conducted in the Solar system, including the deflection angle of light by the Sun, gravitational time delay, perihelion advance, and geodetic precession. The observational constraints are derived by confronting the theoretical predictions with the most recent observations. Among these constraints, we find that the tightest one comes from the measurement of the gravitational time delay by the Cassini mission, which yields 0<P<5.5×10−6. In addition, we also discuss the potential constraint that can be obtained in the near future by the joint European-Japanese BepiColombo project and show that it could significantly improve the current constraints. "

    is spending money on joint European-Japanese BepiColombo to test lqg better than 100tev project

  25. Sabine and Peter,

    now I am an old theoretical physicist, reading your blogs since almost from when they started, but I still do not understand both of you. Allow me to explain the reason.

    It is indeed correct that both theoretical particle physics and quantum gravity have not come up with the correct approach to go forward. And this is so since decades. You both have shown this in great detail, and for this you indeed deserve much praise. You both stress the importance of experiment, the fallacies of wrong arguments, the traps of untestable premises, etc.

    After so many years, it is obvious that in the vast field of possible approaches, the correct one is like a tiny plant still waiting to be discovered among the large number of wrong ones. What today's theoretical physics needs, is a guidance from older experts to younger ones on where to go.

    We have a crisis in theoretical physics, not a crisis in experimental physics. But both of you also explicitly state "don't send me your TOEs". And you also act consequently. Indeed, there are so many bad ideas around. But it implies that you do not give *any* approach a chance. Not even the correct one. Ok, I can understand this attitude as well - time is valuable.

    But if we cannot give answers to younger people, we should at least give them questions. And must give them the correct questions, those that are still open. However, you both have become so negative that you do not even ask the correct questions in your blogs. To be clear, here are the main ones:

    (1) It is clear since decades that gravitation is of thermodynamic origin and that black holes have microscopic degrees of freedom. One goal of quantum gravity is to discover these microscopic degrees of freedom: What are they? How do they make up black holes and space?

    (2) A correct approach to particle physics must explain the fine structure constant or the mass of the electron. Strings failed. Can other microscopic degrees of freedom achieve this?

    The second question is the real test for any TOE. The first might help. It is not required to search for deviations from the standard model to find or to test a TOE. Such deviations might not exist. First of all, we need to understand the standard model itself, with its parameters!

    We need to pass on the right questions to younger people. We need to be careful: We indeed have to tell young people not to take a wrong path. We also have to avoid telling young people not to take any path. But above all, we have to avoid preventing young people from taking the right path.

    1. Thank you Johannes, you really have a skill to use wise words!

      My motto is that when studying the known, there is hiding a coincidence for finding out new unknown.

    2. Johannes,

      There are unconventional research efforts that target the underlying dynamics, flavor structure and parameter spectrum of the Standard Model. They usually fall outside the mainstream paradigms that have dominated the hep-th literature for decades. Granted, some of these ideas are based on wrong or questionable premises, but others explore intriguing ways forward. It is truly unfortunate that accredited academic and research institutions typically reject or simply ignore the bulk of these efforts.

  26. There are now thousands of physicists, ranging from research graduate students to tenured professors, who are pouring over Feynman diagram calculations. They are pulling their hair out and are in a sort of mental agony. They are searching for this holy grail of finding how these diagrams will with Ward identities etc cancel terms and result in a finite answer. With the multiverse and computing generalized YM gauge 4-forms through D-branes the problem is far more vast. If there is anything this is telling us, it that this is not the right method.

    If Sabine Hossenfelder has said one thing right it is that real progress in physics comes when a new theoretical construct solves a conflict, problem or paradox in our understanding. My sense with these problems is entirely the same. Computing lots of perturbation terms or series is not going to give you the final answer. There is some simple statement on the nature of things that will allow us to bypass all of that. That is of course if there is some resolution to this problem at all.

    1. You say:

      “If Sabine Hossenfelder has said one thing right it is that real progress in physics comes when a new theoretical construct solves a conflict, problem or paradox in our understanding. My sense with these problems is entirely the same. Computing lots of perturbation terms or series is not going to give you the final answer.”

      I fully agree. Theorists have realized since long ago that the Standard Model is riddled with many unsettled questions and that mainstream approaches to developing field theory may require a serious overhaul.

      It is really a sad state of affairs that lots of research programs have since underdelivered or failed, with no open admission from academia and influential leaders in the field.

  27. A field which might yield an advancement in fundamental knowledge, at a very modest cost (especially compared to a new high energy accelerator), is condensed matter physics. One of the anomalies that may now be resolved is the Cooper pair mass discrepancy first uncovered by Janet Tate, et. Al, in 1989. The experiment employed fused-quartz spheres of near perfect sphericity, entirely coated with a 1270 nanometer layer of niobium metal. When brought down to niobium’s critical temperature and spun up to a constant angular velocity in the lab the measured London moment disagreed with theoretical predictions, implying a higher mass for the Cooper-pairs than expected.

    Martin Tajmar’s group at the Austrian Research Center in a series of experiments, entailing 250 individual runs, between 2003 and 2006, found that acceleration signals, opposite to the angular acceleration applied to a spun-up niobium ring, were induced on accelerometers located inboard of the niobium ring. Their hypothesis was that within the superconductor gravitons obtain a very small mass producing a considerably enhanced gravitoelectric field much larger than the classical expectation. That changing gravitoelectric field (due to the ring’s acceleration) induces a changing gravitomagnetic (GM) dipole field around the niobium ring. The accelerometers are located interior to the ring (where the GM field would be at its strongest). That changing gravitomagnetic flux, in turn, induces a changing gravitoelectric (acceleration) field in the accelerometers.

    But a paper, dated 22 April 2008, titled: “Search for Frame-Dragging-Like Signals Close to Spinning Superconductors” (arXiv:0707.3806, under gr-qc),, by Tajmar et. Al, raises some puzzling issues. In this series of experiments that involved laser gyroscopes to detect the frame dragging, they found a parity violation; a strong signal only in the clockwise direction. Additionally, the effect did not coincide with the critical temperatures of the superconductors they were using, but were actually above those temperatures. Since this is from 2008 there may have been further resolution of these anomalies, but I couldn’t find anything with a quick search.

  28. The huge laboratories like CERN and Fermilab can only justify their survival by mounting large projects of increasing scope and cost; many small projects won't cut it. This is coupled to "group think," which especially affects young untenured researchers, whose careers will soon be in the sewer if they fail to express sufficient enthusiasm for the lab's plans.

  29. More expensive than the LHC is the James Webb Space Telescope (JWST).
    Nasa's James Webb telescope is the successor to the Hubble Space Telescope.
    It was supposed to have cost $1.6bn and to have been launched in 2011.
    NASA also revealed that the development cost of the telescope would rise from $8 billion to $8.8 billion, requiring it to be reauthorized by Congress, which set an $8 billion cap in 2011. (The total cost of JWST, including operations, is expected to be $9.66 billion.)
    The JWST is clearly not worth the price, but most of that money is already spent, so the best we can do at this point is to continue toward a 2021 launch and hope for the best.

    1. Not sure what you mean. First, no one here is talking about the cost for the LHC. We are talking about the cost for the FCC. Second, the only reason the LHC cost "only" about 10 billion is that the tunnel was reused from an earlier experiment.

      Also, fwiw, the scientific mission of JWST is still better than that of the FCC. So if you think the JWST is not worth the money (which one can debate), you should certainly not build a bigger collider.

  30. Do you think it'd be worth it to invest in accelerator technology? I can't bring myself to easily dismiss the fact that there could be interesting physics at higher energies, but maybe it's time we learned to build better and smaller accelerators? Then all of these claims could be tested and high energy phenomenologists wouldn't become unemployed.

  31. Frankly, the text from Fabiola Gianotti and Gian Giudice reproduced at beginning of teh blog explicitly says: we will find dark matter particles or exclude them as explanation for dark matter [within 100TeV] range. They did not guarantee discovering dark matter particles... Something that certain some of us believe to either not exist or not be the only candidates.

  32. What history actually teaches us is that methods of science change. Problems and practices shift and progress will not proceed along the same paths as before. That is how science -and physics- progresses. Yes, there are lessons from history, but these are certainly not to do it in the same way time and again.

    You often suggest to focus on inconsistencies and quantum foundations - I have been wondering for quite a while now why you wouldn't contribute heavily to these areas? And I am aware of the superfluid DM papers with your doctoral student which are supposedly focusing on an inconsistency.

    1. Right, methods change. This is why I say particle physicists must change their methods. Why wouldn't I contribute "heavily" to the foundations of quantum mechanics. Well, to begin with I am only one person and there are only so many things I can do in a 24 hour day. Second, it's difficult to get funding for. Third, I contribute what I can, also see this.

  33. No, No, No - Particle Physicists are not wasting my money. The US DOD is wasting my money.. by many orders of magnitude. Why not get on their case?

    1. Well, if you want to be technical, the US DOD is wasting their money, not yours. Your taxes are your membership fee for being a citizen of the USA. Like rent, once it is paid, it is no longer "your" money; and we have elected proprietors of this establishment that decide what to do with the membership fees. Including funding misguided research.

  34. If the Higgs Boson was not found, then building bigger and bigger colliders to explore the TeV range would be justified (it seems to me) by scientific hypothesis but indistinguishable from the problem of induction. Then finding the Higgs would be both logically possible and by empirical deduction but until you find it we practice the problem of induction. Prior to the Higgs discovery (in my example) how are these justifications different and why?

  35. "But Carroll argues that he is simply calling for greater openness and honesty about the way science really happens. 'I think that it’s more important than ever that scientists tell the truth. And the truth is that in practice, falsifiability is not a good criterion for telling science from non-science,' he says." -Sean Carroll Caltech.

    Popper's falsifiability is not universally accepted it seems.


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