Wednesday, June 05, 2019

If we spend money on a larger particle collider, we risk that progress in physics stalls.

[Image: CERN]
Particle physicists have a problem. For 40 years they have been talking about new particles that never appeared. The Large Hadron Collider was supposed to finally reveal them. It didn’t. This $10 billion machine has found the Higgs-boson, thereby completing the standard model of particle physics, but no other fundamentally new particles.

With this, the Large Hadron Collider (LHC) has demonstrated that arguments used by particle physicists for the existence of new particles beyond those in the standard model were wrong. With these arguments now falsified, there is no reason to think that a next larger particle collider will do anything besides measuring the parameters of the standard model to higher precision. And with the cost of a next larger collider estimated at $20 billion or so, that’s a tough sell.

Particle physicists have meanwhile largely given up spinning stories about discovering dark matter or recreating the origin of the universe, because it is clear to everyone now that this is marketing one cannot trust. Instead, they have a new tactic which works like this.

First, they will refuse to admit anything went wrong in the past. They predicted all these particles, none of which was seen, but now they won’t mention it. They hyped the LHC for two decades, but now they act like it didn’t happen. The people who previously made wrong predictions cannot be bothered to comment. Except for those like Gordon Kane and Howard Baer, who simply make new predictions and hope you have forgotten they ever said anything else.

Second, in case they cannot get away with outright denial, they will try to convince you it is somehow interesting they were wrong. Indeed, it is interesting – if you are a sociologist. A sociologist would be thrilled to see such an amazing example of groupthink, leading a community of thousands of intelligent people to believe that relying on beauty is a good method to make predictions. But as far as physics is concerned, there’s nothing to learn here, except that beauty isn’t a scientific criterion, which is hardly a groundbreaking insight.

Third, they will sure as hell not touch the question whether there might be better ways to invest the money, because that can only work to their disadvantage. So they will tell you vague tales about the need to explore nature, but not ever discuss whether other methods to explore nature would advance science more.

But fact is, building a large particle collider presently has a high cost for little expected benefit. This money would be better invested into less costly experiments with higher discovery potential, such as astrophysical searches for dark matter (I am not talking about direct detection experiments), table-top searches for quantum gravity, 21cm astronomy, gravitational wave interferometers, high-precision but low-energy measurements, just to mention a few.

And that is only considering the foundations of physics, leaving aside the overarching question of societal benefit. $20 billion that go into a particle collider are $20 billion that do not go into nuclear fusion, drug development, climate science, or data infrastructure, all of which can be reasonably expected to have a larger return on investment. At the very least it is a question one should discuss.

Add to this that the cost for a larger particle collider could dramatically go down in the next 20-30 years with future technological advances, such as wake-field acceleration or high-temperature superconductors. In the current situation, with colliders so extremely costly, it makes economically more sense to wait if one of these technologies reaches maturity. Who wants to spend some billions digging a 100km tunnel when that tunnel may no longer be necessary by the time the collider could be be in operation?

Anyone who talks about building a larger particle collider, but who does not mention the above named issues demonstrates that they neither care about progress in physics nor about social responsibility. They do not want to have a sincere discussion. Instead, they are presenting a one-sided view. They are merely lobbying.

If you encounter any such person, I recommend you ask them the following: Why were all these predictions wrong and what have particle physicists learned from it? Why is a larger particle collider a good way to invest such large amounts of money in the foundations of physics now? What is the benefit of such an investment for society?

And do not take as response arguments about benefiting collaborations, scientific infrastructure, or education, because such arguments can be made in favor of any large investment into science. Such generic arguments do not explain why a particle collider in particular is the thing to do. I have a handy list with responses to further nonsense arguments here.

A prediction. If you give particle physicists money for a next larger collider this is what will happen: This money will be used to hire more people who will tell you that particle physics is great. They will continue to invent new particles according to some new fad, and then claim they learned something when their expensive machine falsifies these inventions. In 40 years, we will still not know what dark matter is made of or how to quantize gravity. We will still not have a working fusion reactor, will still not have quantum computers, and will still have group-think in science. Particle physicists will then begin to argue they need a larger collider. Rinse and repeat.

Of course it is possible that a larger collider will find something new. The only way to find out with certainty is to build it and look. But the same “Just Look” argument can be made about any experiment that explores new frontiers. Point is: Particle physicists have so far failed to come up with any reason why going to higher energies is currently a promising route forward. The conservative expectation therefore is that the next larger collider would be much like the LHC, but for twice the price and without the Higgs.

Particle physics is a large and very influential community. Do not fall for their advertisements. Ask the hard questions.


  1. Dear Dr. Hossenfelder
    There is a paper about the social and economic impact of the LHC by the OECD in case you haven't seen it. Quite interesting I think:
    There is one part I particularly like:
    "Attempts have been made elsewhere to develop analytical methods, and to gather appropriate data, in order to derive statements of the form “X currency units invested by governments in fundamental research generates Y currency units in additional GDP (or jobs, or increases in quality of life indices)”. But these attempts (and results) have been criticised on methodological grounds, and the Global Science Forum decided not pursue a quantitative study of this type."
    I agree with them. So much for any form of usable ROI.
    I pretty much changed my view during the last few month and I read quite a few of the proposals published here:
    Not all countries or groups are all that favorable towards a new machine. Therefore the FCC isn't a done deal at all.
    How about relocation half of CERN to Saint-Paul-lès-Durance? That could accelerate other important (at least just for saving the world) experiments?

    1. Christian,

      Yes, the EU has also done a variety of studies on the impact of investing into R&D. There are a number of other attempts that you find on the arXiv.

      But as I have said before, you don't need to know an absolute ROI to make statements about a relative ROI. More scientific promise for less money is better even if you cannot quantify the payoff in absolute terms.

      Yes, that's right, not all particle physics is high energy collider physics. But not all research in the foundations of physics is particle physics either. The idea that particle physicists decide whether to do particle physics or particle physics strikes me as too silly to even discuss.

      In any case, as I have hopefully made clear, my major issues are

      (a) the community does not fix problems that waste money but they want more money and

      (b) hype and lobbying.

      I worry about the latter not because I think people may accidentally believe it, but because I am sure they will not believe it, unless they are already believers. In other words, people who go around and proclaim we need a particle collider but fail to mention the obvious reasons against it do big damage to science.

  2. I'm a computer scientist not much into physics, so I don't know the matter well.

    But didn't the experiments at the LHC produced a lot of inventions, patents and spin-off products that entered our lives?

    Would love to read your opinion on that side of the story.

    1. Ahmet,

      It is certainly the case that pouring money into developing large, supercooled magnets and high precision detectors has the occasional technological spin-off. It would be shocking if that wasn't so. The question you should ask, however, is this: If the spin-offs are what you are really after, wouldn't it be better to invest into this in the first place?

      Besides this, as I said above, the case about potential spin-offs can likewise be made about any other large-scale science investment. So it's really not a reason to build a larger collider.

    2. Ahmet,
      There is certainly an impressive list of spin offs, knowledge transfer and startups from CERN - see for more details.

      Dr Hossenfelder points out spin offs etc. can be expected from any large scale science investment. I'd go further and generalise this to say spin offs are almost inevitable from any project which comes up against the currently available technologies. As an example take cross head (aka Philips) screws - 'invented' to allow higher torque settings to be used in automobile mass production.
      Whether the expectation of known or unknown spin offs should contribute to the decision to fund a project is complex. Some (unknown) spin offs will arise due to the need to overcome unseen problems encountered during the project, others (known) can be foreseen - though the practical solution and any potential uses may be unclear - from the project requirements.
      I have this vision of a neolithic fashion designer approaching their tribal elders with a project to produce a fur coat - warm windproof etc. - but to do so they'll need to overcome the problem of how to join fur pelts together. The tribal elders have to approve the time and effort needed to sort out a solution. Given approval the neolithic Calvin Klein comes up with a needle and thread - the known problem has generated a solution which has the (unexpected and unknown) spin off which is still 61000 years later used in many areas of our society, not just fashion.

  3. Dear Dr. H,

    Can you please detail your stand on the dark matter direct detection experiments? Do you think they are poorly motivated as well? How about the Axion searches?

    1. C,

      The reason to believe in WIMPs an axions are arguments from naturalness or a numerical coincidence known as the WIMP miracle. These are metaphysical principles and are belief based, and therefore unscientific.

      Even if you think that the first searches for WIMPs and axions in the 1980s were worth a shot, tuning these models every time an experiment has not found the particles has not made the predictions any more reliable.

      The short answer is, yes, these experiments are poorly motivated. On the other hand, they are not as expensive as a larger particle collider, so I think they don't require as good a motivation.

  4. A few copy edits:

    Par 5; "A sociologists would be" --> "Sociologists would be"

    Par 5; "But for what the physics is concerned" --> "But as far as physics is concerned"

    Par 7; "for just to mention a few" --> "just to mention a few".

    Par 8; "And that is only for what the foundations of physics are concerned" --> "An that is only as far as the foundation of physics is concerned" Or maybe "And that is only considering the foundations of physics".

    1. Thanks, I have fixed that! Will try to keep this in mind...

  5. It is such a refreshing change to hear articulate reasons why any huge scientific endeavor should be scrutinized with regards to the overall benefit to humanity. We are more likely to die of starvation once we destroy the ocean than the angst of not knowing if physics models are complete to the degree of precision being sought. I studied the quantum theory of semiconductors and manufacture computerized gasoline detectors to protect drinking water and physics works just fine with what we already know.

  6. Sabine,

    re: "If we spend money on a larger particle collider, we risk that progress in physics stalls."

    in the 2030-40 timeframe after HL-LHC completes its run do you consider spending $7 billion to upgrade LHC magnets from 8.3 T to 16 T thereby increasing collision energies from 14 TEV to 27 TEV to be "building a larger collider"

    the 27km tunnel and most of the equipment will be re-used. only the magnets and injectors will be upgraded.

    IMO $7 billion to explore energies from 14 TEV to 27 TEV for HE-LHC is reasonable.

  7. Do you not accept the recent European effort to evaluate the future of particle physics, nor the ongoing preparation for the five year review of the same topic in the U.S. as good faith efforts to ask precisely the question you claim you want answered? (This question being: "What research approaches should we pursue in the next few decades?")

    Certainly in the U.S. possibilities beyond a VLHC are being discussed.

    1. Don,

      What do you mean with "not accept"? Do I "accept" that particle physicists hold meetings to make a strategy about particle physics? Sure. What is there not to "accept"? But is this the discussion we need to have? No.

      As I already said above, if you ask particle physicists if they want to do particle physics or particle physics the answer will be particle physics. I don't need strategy reports to figure that out.

      The question I asked is not "what particle physics should we do in the next decades" but "what should we do to advance the foundations of physics". And, in case you missed the point, asking particle physicists may not be the wisest thing to do.

      I told you this previously, but particle physicists seem slow to get the message, so here we go again. This community has a problem with information processing that it isn't doing anything about. This alone is a major reason to not throw further money at them until they have done something about it. What have particle physicists learned from the past decades? What have they done to prevent fads from taking over again and wasting further money? What have they done to prevent the next hype cycle? The answer is: Nothing.

  8. Dr. Hossenfelder
    You do not have to convince me (anymore). I just have a problem with the use of ROI. It is after all a number and therefore has to be quantified in some way or another and it does not apply to investments of a country (and I have yet to find the relative ROI, but I think I know what you mean).
    If we would use ROI in this case, we would have to use standard bookkeeping techniques for a company, but CERN is an international organisation and therefore ROI just does not work, because a ROI - if we could quantifie the results in any way, which I doubt due to the complexity - would always be positive, even if nothing is found. Some of the proponents of the FCC even argue that finding nothing is a good result (Yeeehaaaa, awesome, now we finally know that the last 60 years were a complete waste of time and money and we can finally start looking elsewhere. Cool! Positive ROI). What you can do, is compare benefits of results. Getting ITER to work is much more pressing than finding out that we looked at the wrong corner (just my pet example, I know).
    Hype and lobbying. Well that's democracy. There will always be those who point out the benefits and those who point out the shortcomings. In the end the gouvernements will decide, if they want to commit to the FCC. There is a high probability that the FCC will be build (but not 1), but that is the way it works and frankly I don't want it otherwise, even if the next generation of particle physicist will call the current generation morons for deciding something that is with even higher probability, utterly useless. But frankly, whoever is going to decide on the FCC, the decision will be an informed one where all the pros an cons are taken into account (Yes, I am helplessly democratic), despite all the lobbying and hype. I remember the talk in the Royal Institution and I was pretty annoyed about it, because these guys just don't understand, how financing something like the FCC works. If I had to decide after this talk, I would rather have bought an aircraft carrier. Economics isn't always an exact science, if some aspects can even called science, but some things work and sometimes even physicist should listen to an economist. They did not help their cause.

    1. Christian,

      I understand your objections to the ROI. I will admit that personally I don't think it's a particularly useful measure to evaluate basic research either. If anyone has a better argument, that's all fine with me. My issue is primarily that the discussion isn't even taking place.

      Regarding hype and lobbying. Science isn't a profession like any other. Scientists are not selling products or offering services. They have the task to find out how the world works. If they hype, if they lobby, if they market, they corrupt the principles of their own profession and, ultimately, hinder progress.

    2. Christian,

      Let me add, that regarding the decision for the FCC, I am not at all sure that the decision will be an informed one.

      I am saying this because I have, in the past year, had a number of truly shocking exchanges with experimental particle physics who, by and large, actually did believe the arguments coming from theoretical physicists about the prospects of finding dark matter or supersymmetry. I am afraid that many of them still believe it.

      I don't blame them because, of course, much of science is highly specialized and relies on division of labor. They trust what the theorists say. Even if they personally don't buy it, it's good enough for them to repeat it and bring it up for funding decisions. And so here is the thing.

      Theorists are looking for new arguments for why there is supposedly something weird with the Higgs that requires further study. They do this as we speak, basically, because they need such an argument to get further funding. This, needless to say, is not a good initial condition to arrive at correct conclusions.

      Now, there is a chance that someone will actually come up with a good argument why the Higgs needs further study. If so, fine. I'll turn around 180 degrees tomorrow in that case and become the greatest fan of the FCC if there is a reason why it would pay off.

      What is much more likely, however, is that they'll come up with another nonsense reason, find enough people to believe it, and the sheer number of people who believe it will convince those who finally make the decision that there is something to it.

      That's a real risk, and it's a risk that particle physicists are not doing anything to prevent.

    3. I see your point and that danger is real (Sounds a bit like Sheldon Cooper making fun of the experimental physicist - and lower life form - Leonard Hoffstetter).
      There is also the danger, that it's funded because it is CERN. They played their cards pretty good from a marketing point of view. But in a way I think CERN has lost its mojo it had 30 years ago.
      But let me ask you this. When the funding for the LHC was decided, what has changed since then? Are the arguments at the same "uncertainty" level as then? Are the people who actually prepare the papers for the politicians in the different countries better informed? Do they know both sides? Is "something weird" enough?
      I think, that the FCC has much less chance to get the funding than the LHC many moons ago, because the information is available much easier than it was in the antediluvial time before HTML.
      But then again, the situation is somewhat similar, because then the SSC was on the horizon and now the Chinese want to build one. So the deciding body might want to build the FCC, just to be in the game. Looking at the Chinese project, they have underestimated the cost quite a bit, though the situation could be in the end, that the Chinese drop out (like the US from the SSC) and CERN could be again on top, just for the sake of having the longest.
      Many other factors decide the FCC, not just the research results.
      In the OECD paper, there are some interesting informations, why for companies building the FCC might not be as interested in the knowledge transfer as one might believe (no, that paper is not only about how to measure/forecasting the benefits). Expected spin-off will have a much lower impact on the decision today. One reason is, that the problems companies work on today, are much more "common" or just in another field.
      I don't think that anyone in the field expects the FCC making a big impact on quantum computers or anything else. CERN isn't even on top of the game regarding AI. They are much too big to move as fast as a game programmer today.
      Even if the theorist are playing their selling game very good, I don't think that will be enough.

    4. Christian,

      What has changed is that for the FCC there is no good prediction that it would see anything that would help advance theory development. The Higgs was a good prediciton. With the Higgs found, the standard model is complete. There is the issue with the neutrino masses, of course, but that doesn't require solution until ten orders of magnitude of energy higher.

      So, there is really no good reason to build the thing. If it wasn't all that costly you could say, well, you never know, let's just test the SM somewhat further. All right, there's that. But for that amount of money you need a better motivation, imo.

      Yes, of course there are political factors besides the scientific ones. I'm not the right person to ask about this. Personally I don't think the Chinese will go ahead with their collider plans. The reason is as follows.

      The Chinese, in my impression, seem to have two main goals with the collider. One is to bring international top researchers into the country. The other is prestige. You can import people with many large scale investments into science, think fusion, telescopes, quantum computing, and so on, so really that's not a good argument for a collider.

      What's good about the mega collider is that they might well be the only nation to have one. On the other hand, they risk being the first nation to invest lots of money into a high energy particle collider that doesn't find anything new, which would make them look stupid. I don't think they will take this risk.

      And in any case, for all I know CERN will have to make a decision about whether or not to push forward with the FCC plans in spring 2020, while the next 5-year plan of the Chinese isn't due until 2021. So the Europeans can't wait for the Chinese to make up their mind.

      When it comes to CERN, I think you are underestimating inertia. Particle physicists are not making a good case (in fact, they are pretty much not making any case), all right. The reason they don't bother is that they know as well as I that they have a good chance to get money just because they already have money.

    5. Dear Dr. Hossenfelder
      Yep, we are on the same page here. I might underestimate CERN's inertia, but CERN might overestimate it. The Higgs-hype is pretty much over. Ask anybody in the street, what "The Higgs" does. Apart from God particle, you won't get any response.
      I do count on envy. Some particle physicist might think, that CERN has had its run, now somebody else should get a shot. In the ECPP proposals were quite a few that do not need the FCC and some of them are vastly underfunded.
      Whatever, we will see in '20 what happens and with past experience the FCC will be at least 10 years late (thank god it's not in Berlin, otherwise we would still talk about first beam on the LHC). Around 2050 I do not care anymore and ITER should be not more than 5 years away from first plasma.

  9. Put $10 billion into Alzheimer's research; find a solution; use the resulting savings in future health care expenditures to fund a collider and 10 other research projects just as big.

  10. Dr. Lee Smolin's recently published book "Einstein's Unfinished Revolution" makes the clear point, accessible to the general public, that fundamental work on the foundations of Quantum Mechanics needs to be accomplished. It clearly echoes your own book and postings.

  11. I have no problem with beauty in physics. The variational principle is beautiful. Gauge invariance is beautiful. So is Dirac's electron equation.

    But those ideas have paid off, whereas string theory and supersymmetry have not. They're also not beautiful, mainly because their complexity betrays an underlying ugliness.

  12. Sabine wrote: the cost for a larger particle collider could dramatically go down in the next 20-30 years with future technological advances

    That's an interesting point.

    Sabine wrote: If you encounter any such person, I recommend you ask them the following . . .

    I've seen the responses to those questions in this blog. It's sort of like asking Trump supporters tough questions about Trump. Or worse, asking Trump himself about his own statements and policies. It seems like an exercise in futility.

    That being said, in a blog like this, at least the questions and answers are on the record, for anyone to see and make up their own mind. But it sure seems hard to persuade anyone to change his mind or even take the questions, or the facts, seriously. :-)

    1. Tbh, I don't so much write this to convince anyone, I primarily write it to make my position clear so I can still look in the mirror tomorrow without flinching.

      It is beyond me how scientists can ask for $20 billion without even thinking about the reasons why there hasn't been progress in their field for 40 years.

      Especially those who want to shame other scientists into silence by claiming any scientist needs to be supportive of any major investment. Let me not name names. If you know who I mean, you know who I mean.

      And on the other line I have a climate scientist who can't get funding for making better predictions. I'm serious. That's the world we live in.

  13. I guess it is not clear to me that this situation is that dire. I am not sure all of physics will wither away because of the FCC. I am still somewhat on the fence about this. I can honestly see points either way.

    1. Lawrence,

      Not any time soon, no. But progress in physics is ultimately driven by breakthroughs in the foundations. If atoms hadn't been discovered, there wouldn't be any condensed matter physics today. If we didn't understand light, there wouldn't be any interferometers. All electronic gadgets we use today build on quantum mechanics, which is technology that benefits all areas of physics.

      Now, we aren't done squeezing the existing knowledge and can go on squeezing for some while. But returns are already diminishing and without any major breakthroughs, we'll just continue to incrementally improve a digit here and there.

      I know that this offends a lot of people, but I hope you will forgive if I say that the foundations of physics are essential to progress overall. This doesn't only concern physics, but all other disciplines. Think of any imaging method used in the life sciences. X-rays, MRI, spectrocospy, electron microscopes - it's all physics.

      So this is why it matters we get the foundational work right. (And in any case, if you don't think it matters, this isn't a reason to build the FCC either.)

    2. I turned away from particle physics in graduate school for a couple of reasons. One of them being that while I found supersymmetry fascinating, I saw it as a relationship between quantum statistics and spacetime boosts and physics. I had a hard time seeing supersymmetry as having much to do with the standard model, but more to do with quantum gravity. The other is the whole framework for what was to be observed seemed to be largely worked out. The standard model was put in place around the time I was in 1st grade and there seemed to be few compelling reasons to consider theory beyond this. It appeared that particle physics had rendered itself somewhat uninteresting. I then chose gravitation instead, which turns out to be about as employable in that field as is linguistics.

      My sense is that if we are to probe physics in the 100TeV range that we might consider finding new ways to accelerate particles. Laser-plasma systems, such as the plasma wake as I recall it is called, might be considered for development. It is not hard to derive a longitudinal electric field for an EM wave if the dielectric constant ε = ε(E) or ε = ε(D). The equation is sometimes called the cubic or nonlinear Schrödinger equation. In this way a proton can be pushed with a much higher field density than we can with RF cavities used today. In that way a future LHC+ machine might be made that is comparable in size to 1970s accelerators.

    3. I did not have time to write everything I wanted to.

      When it comes to technology there are still some possible impacts that particle physics can have. Dark matter detection may play a role in neutrino communications. Detectors that involve a putative DM weak interacting particle that measure phonons from such interaction may pave the way for neutrino signals and communication. Of course a lot has to be worked out, such as cryogenic cooling by solid state devices, which are in a research stage. If means can be made to produce neutrinos at low energy in small devices we may begin to get neutrino transmission and reception.

      Of course there are a lot of things that may not happen. In the movie 2001 A Space Odyssey there is "Luna City" and large interplanetary spaceships. Well, so far that has not happened, and it seems a long way off. We do not have flying cars or jet packs. Robots though are starting to make appearances. Nuclear fusion seems to be as far off as it ever was, in spite of New Scientist reports to the contrary.

      We must realize that with all the techy stuff with the internet about 40% of it is the dark web that involve criminal activity. Of the above ground internet over 25% involves pornography about an equal amount games and then most of the remaining is social websites. We call it progress.

      Of course from the perspective of civilization we do need to have great discoveries and breakthroughs. This is the main way we can compete against ignorance. I am not sure about the future here. There are of course other things that can serve this role besides physics. The discovery of an extrasolar planet that bears unmistakeble signatures of biology would get people excited.

  14. I got an idea ... let's abandon the Copenhagen interpretation and start over.

  15. Null results are also important but they don’t strengthen the arguments why the positive results will be found where they think it is now. They could be just as wrong as before, or more likely to be wrong now. Spending huge money to test predictions of theories that have not been successful is unwise. Physicists don’t think in terms of cost and benefit. It’s the job of economists. Yes they are lobbying.

    Economists and policy makers may not have a good grasp of how solid are the predictions, the benefit side of the equation. When there is an EU hearing on the FCC, you volunteer as resource person. It will be for the good of society.

  16. Particle physicists which want a bigger collider are hoping the public is even dumber than when they sold the LHC to them. The argument goes like this.."The LHC is old technology,just like your iPhone, we need to upgrade to the new model to make new discoveries. Don't ask questions about a complex field that you don't understand. We're the professional scientists, give us the money and we will find the answers." For years I would hear that the reason the average citizen needs to learn science in public schools is so they can make an informed decision about funding projects just like act as a check and balance on radical science claims that need more funding. Well, it doesn't get any simpler than this.. thanks to the failure of the LHC to find anything new beyond the Higgs boson...if the other predictions of exotic new particles didn't come true I think Joe Public should be as knowledgeable about deciding funding on a new collider as the current Presidents science advisor (if he has one) would be. It has sadly come to that, were our public education (which includes understanding the scientific method) is just as good as any expert's opinion.

  17. So, I take your arguments to another field:
    Dark Matter searches have been going on for quite a while. Total costs could also be in the billion by now. They haven't found anything. So, let us stop it?

    1. Quant,

      I already commented on this above. Current direct searches for dark matter are not promising for the same reason as the FCC is not promising: There is no reason to think the postulated particles actually exist. The arguments for them are based on metaphysical principles that are essentially appeals to beauty. There is no good scientific reason to think this is correct.

      Also, as a matter of fact, it has not worked for 4 decades.

      Different matter entirely, however, with astrophysical searchers that collect evidence about the behavior of dark matter (or its alternatives) through its graviational influence. Collect more of that information, at better quality, and you might be able to pin down what particle it is (or conclude it's not a particle). Then you would know better what Earth-based experiment could test this particular hypothesis.

      On the other hand, direct dark matter searches are far less costly than a mega collider, so you might not want to put the bar quite as high.

    2. Sabine,

      Current direct searches for dark matter are not promising for the same reason as the FCC is not promising: There is no reason to think the postulated particles actually exist.


      Different matter entirely, however, with astrophysical searchers that collect evidence about the behavior of dark matter (or its alternatives) through its graviational influence.

      The logic here eludes me. There is no reason to think the postulated dark matter particles exist but you want to study the behavior of those same particles you don't think exist?

    3. bud rap,

      Please read what I wrote carefully. I wrote there is no reason to think the postulated particles exist. I am referring to the *specific* particles that were postulated whose existence you could measure at the FCC. A particle collider is not a good machine to find any kind of particle. It is good to find specific types of particles. I am pointing out that we have no reason to think dark matter is of this specific type. If it is a particle to begin with.

      I didn't say I want to study the behavior of those particles, I said collect more details on the already known observational discrepancies, until you can either pin down what type of particle it is (or figure out that it's not a particle).

  18. I'm just a layman who is curious about the Universe, so I read all this stuff.

    It's my layman's understanding that you do science by:

    1) Positing a theory. The theory HAS to be testable, otherwise it's not science, it's closer to metaphysics.

    2) Next, you devise one or more experiments to prove or disprove your theory. If you don't have the technology to test your theory you create it, as with the LHC, or you wait for a future time when you will may be able to create a test.

    From what Sabine says, the new collider is not this at all. It's a hugely expensive roulette wheel that people want to have to keep their careers. They want to just spin the electromagnetic wheel and see which numbers come up.

    1. Mike,

      As I explained here, a scientific theory has to be testable, yes, but just because a theory is testable doesn't mean it's scientific. All kinds of wild guesses are totally falsifiable, so that is an exceedingly poor criterion.

      So, what you say is correct, but not because the theories that particle physicists invent are not falsifiable. Most of them are falsifiable. Indeed, they have promptly been falsified. The problem is that they were not reliable predictions to begin with.

    2. 👍
      I was just trying to say that testability is necessary. I understand it's not sufficient.

  19. Here's a cautionary tale that may be applicable to the current discussion. There are two very enjoyable reality-based television shows on cable (I think they're on the Discovery Channel or something similar). One is called Engineering Marvels, or words to that effect, the other is Engineering Catastrophes. A short while ago, I saw on Engineering Marvels a glowing tribute to the seawall project in Venice designed to prevent the constant flooding currently afflicting the city. It described the project's ambitious scope, state of the art design, and insane cost, and had fabulous footage of the huge panels designed to rise up out of the sea to block the encroaching tidal surges. It was inspiring. A few weeks later, I tuned into Engineering Catastrophes to see...the same project! Turns out the paint on the panels doesn't resist corrosion, the joints are getting clogged with sand, and various ocean-dwelling critters are mucking up the works. The whole contraption looks to be as good as useless. It's still being built, at a cost of countless billions, with no end in sight because there's no "Plan B" thanks to the enormous cost, time, and resources already invested. Draw your own conclusions...

  20. Bruce Rout,

    True Dat... /DropsMic

    Ok seriously now, As much as a agree with the above I think you're going after the wrong target. It's too esoteric for the lay public (and me too for that matter).

    What we should be telling the uninitiated is that there is no such thing a "observation" or "measurement" in QM only interactions.

    To be more specific we should insist that all interactions change the level of correlation between quantum systems. In QM the useful information that results from a experiment is the combination of the nominal result AND the error bars. We can then move to explaining that the correlations between systems are the error bars and that we have discovered some hard limits on the error bars for sufficiently simple quantum systems.

    I like this twist because I think it eliminates the "superposition collapse" myth. It also guides people away from doing the observation-->observer inference which often leads incautious minds to start rumination on meta-physics... which I think is 'a long road that don't-go no-where'.

    As to many worlds or any sort of infinite inflation to solve ones aversion to fine tuning, why can't people see that nakedly inserting an (unprovable) infinity into an argument doesn't make it stronger?

  21. @Sabine
    It's not the first time you cite nuclear fusion as a project where more money should go, instead of a next collider.
    This is very ill-thought indeed. Nuclear fusion has a terrible reputation among politicians (indeed, among scientists from other fields) because it keeps promising clean energy "within the next 25 years", and this for about 50 years now (talk about lies and hype...)
    It is estimated that, since the 50s, only the US have spent about 30 billion dollars on fusion. Counting the rest of the world might almost double that figure. And, with all that, we still run our old fission power plants.
    I fail to understand why you would like to pour even more money there.

    1. Opamanfred,

      I'll write some more about nuclear fusion in the future, then maybe you will understand. Let me just say that I think the investment is well justified. Frankly I think that given the enormous potential payoff if would easily justify much more investment.

    2. You are falling into one of your own pitfalls. The question is not whether fusion has "enormous potential payoff". The question is (like for the next collider) whether these tens of billions of dollars are well invested in fusion, or should rather be better invested in other types energy research.
      These are the terms into which you phrased the question about the collider, and should remain the same for fusion as well.

    3. If you think that is what I have said, you misunderstood. As I have explained many times in case of the FCC the situation is that we know it is extremely costly compared to other investments in the foundations of physics, and we know that investing in other directions is currently more promising for progress, which leads to the conclusion that a larger collider is not a good investment in the foundations of physics. It adds to this that it is not a good societal investment either because there isn't much you can do with particles that decay in less than a nanosecond.

      If you believe you can make a similar argument against fusion power, I would be curious to hear it.

    4. I will make an argument against fusion power, at least until the physics community clean-up their theory. That means (please) revisit the plasma physics that suggest fusion is possible not just plausible, and stop simplifying a fusion hypothesis with simplifications and omissions to render more beautiful mathematics.

      A physicist assured me to achieve fusion ignition on a laboratory scale does not rely on quantum tunneling (QM) or Special Relativity. Great, that leaves first-law fundamentals to guide us. Fusion, I have read, occurs in the sun's core through quantum tunneling of (sparse) Hydrogen nuclei but on a grand scale. By eliminating the scaling necessary for fusion in the sun's core, and rather dirty fusion assisted by a secondary fission as in a thermonuclear weapon, that should simplify our laboratory experiment. Another physicist assured me ignition should occur when the rhoTtau is dense enough (rho), hot enough (T) and confinement time long enough (tau). So far so good, the task appears simpler now.

      But what if first-law fundamentals show us that fusion cannot occur? What-if a comprehensive first-law assessment of an energy balance shows there simply isn't enough energy in the system to allow fusion to occur due to losses from neutron escape, thermal leaks and energy losses the beautiful math left out? Has anybody actually done-the-math to confirm the predictions for fusion ignition? No, I don't mean sophisticated 3D code analysis, and no philosophical arguments to dispute the meaning of '=' as an abstraction of energy balance (thank you First Name Surname). We need a sanity-check. Let's apply first-law fundamentals before we engineer D/T targets for RT instabilities, or build bigger and bigger Tokamaks.

      Given the above I eagerly anticipate Sabine's future post on the promises of fusion, the 30-year kind of-course.

  22. Sabine,

    for your next blog post, what do you think are the most important future particle physics experiments HEP and even QG should invest in?

    future physics experiments in HEP that should be funded before any talk of FCC 100TEV scale collider

    obviously future electron/neutron EDM should be on this list

    1. neo,

      I have answered this question many times: I cannot as one person replace the work of a whole community.

  23. Building a new particle collider must have a purpose. For example the discovering of new phenomena. Or a better understanding of the way our universe acts (unification of particles and forces). Unfortunately the latter is fundamentally impossible with the help of phenomenological physics. So it is about new particles… That’s not quite convincing.

  24. Sabine, you are right regarding the particles: boring topic. Game over, the same with cosmology - a good seller for the general public looking at the heavens via tv show. But read the BACKPAGE of APS News from August 2018. The author is Katepalli Sreenivasan, a man socialized in Idia who has run for decades the Princeton Superpipe to study turbulence. He is stating that he is often asked as to whether it is true that "we" cannot compute the turbulent flow through a water pipe based on first principles - althogh flying to moon and walking trough exotic particle zoos. There's a contradiction.
    We need to realize that the so-called WEST is the youngest part of humankind, still close to simple barbarians when compared with the much older civilization of Asia where cooperation and solidarity are key to survival in an environmenr of mighty rivers etc. - but with huge chances, too. There only those survive who develop somehow sort of cooperative and solidaric ethics/habeits. Others simply dye off ...
    The physics crisis is simply embedded in the general civilizationanl crisis of the WEST.

  25. I think one should put things into perspective:
    The nuclear-armed nations spend about US$100 billions a year on their nuclear forces. These days hardly anybody seems to care anymore even though the doomsday clock has been set to 2 minutes to midnight. Why care about US$20 billions spent once where in the worst case we find no new particles, which is nothing compared to the eradication of mankind as result of a nuclear war apocalypse.

  26. Sabina, what is yourtake on the Elctron-Ion Collider planned in the USA, probing the inner structure of protons and neutrons?

  27. What's the point of the comment about quantum computers and fusion? We do have the former; IBM will let you run code on theirs of you ask nicely, and over the next few years the major tech firms will scale these up unless there is some unexpected problem like dynamical wavefunction collapse. And the latter requires trillion Euro sized investment, but is achievable. CERN isn't competing with these enterprises, but rather all of the rest of basic science that will give us the quantum computing and fusion of tomorrow.

    1. Wibble,

      Needless to say I was speaking of quantum computers that can do better than classical computers and that are actually good for something. You could similarly say we have fusion reactions, it's just that those happen to not have a positive energy output. Well, yes, let's see how they scale these up.

      I know that CERN high energy particle physics is a more long-term investment than that. Why do you think you have to inform me of this? This doesn't mean you do not have to justify the investment. By your logic, if you invest in the farthest future, say 10 billion years from now, then any investment is justified. This is just economic nonsense.

    2. I don't think that we disagree that CERN is a bad bet, but my understanding on 'real world' quantum computing and fusion is that these have moved in recent years to be much more problems in engineering than fundamental science so that selling these as a possible return on investment in fundamental physics is risky. Advanced materials, biophysical insight, and quantum technology generally seem much more likely to arise as benefits from investment in multiple, cheaper, fundamental physics questions that we probably agree is a better strategy than a new collider.

  28. Whenever there is a large community representing and practicing any given highly skilled profession, there is a need to support that profession with a stable source of funding. If that high skilled profession is deprived of that funding base, then the profession will decline and eventually die. Examples of this process is fusion physics with funding that comes from fusion reactor development, nuclear engineering with funding coming from the deployment of nuclear reactors, aerospace workers who depend on funding for rocket development and space missions, astrophysicists with the deployment of large telescopes, defense workers who depend on the funding for weapons systems development, or particle physics with the fielding of large particle accelerators. Some organization has to sign the paychecks or the young people who are deciding what profession to devote their lives to will avoid a choice that has no funding base. By killing the funding, you kill the field.

    1. Axil,

      IN 1925, there was no field of experimental high-energy particle physics (Lawrence invented the cyclotron in 1929-30). In 1965, there was.

      Somehow, we got going from scratch during those four decades.

      If we "kill the field" and it seems necessary to start it up again, we can do so. It might even be that the reboot would bring fresh new ideas that the old geezers overlooked.

      If you want to be more quantitative, you should figure in the cost of keeping the field going for decades when there is really no point to it vs. the start-up cost of starting afresh.

      In essence, you are making a "too big to fail" argument. Experience suggests that institutions that are "too big to fail" actually need to be put out of their misery and replaced by fresh new growth.

      Anyway, try refining your argument along the lines I have suggested, compare it with experience in, e.g., high-tech industry (IBM vs. Apple, RCA vs. Intel) and see where it leads.

    2. When all the experts (aka old geezers) in the dying field are gone, who has the wisdom and the background to inform the decision makers that the field requires a comeback?

      In other fields, it is obvious that a field needs to be reactivated. Anybody can recognize that a new weapons system or energy source must be developed. But in particle physics, who is going to determine that a new particle is absolutely needed to the tune of hundreds of billions in startup money?

    3. The problem with "too-big-to-fail" is, they are too big to fail. 2007-2009 we have seen, that no matter what, these organisations will be saved.
      That begs the question, is CERN too big to fail? Would not building the FCC kill a whole field? Or to turn it around: does a whole field depend on one 100 km experiment? If that is the case, that field is bound to disappear anyway so why not getting it over with. I don't think that too big to fail applies to the FCC.
      If it does, we should under no circumstances build the FCC, because it would aggravate the situation. Too-big-to-fail is bad. Throwing money at it just to keep it alive is the worst possible solution, worse than not throwing money. Radical change must be part of any solution and the FCC would not be the change needed.
      Dr. Hossenfelder, would you mind to give me a hint about IBM vs. Apple and RCA vs. Intel. I don't see any relation to the too-big-to-fail problem in the first pair and no connection between Intel and RCA. I just don't get it.

    4. @Axil: We haven't been to the Moon for nearly 50 years. And yet, despite this fact, NASA is currently investing in the technology to send people to the Moon again. It will take some money to reinvent the technology, but compare that with the money it would have taken to keep sending people to the moon over the last 50 years. And would we really want to send people to the moon using 50-year old technology today, anyway.

      There may be good arguments for building the next big accelerator, but if this is the best argument you can come up with, Sabine is absolutely right and it shouldn't be built.

    5. Going to the moon and later to Mars is an ego trip for more that a few current politicians and multi-billionaires. Most of the Moon and Mars tech is privately funded anyway. Space tourism is about to become a money making proposition. There are millions of star trek and star wars fans pushing the romance of space travel into the public political domain.

      Nobody has written sci-fi books or movies about discovering a new fundamental particle. The public does not care about particles. The concept and uses for a new fundamental particle is not tangible in the public mind. When the level of brain power needed to understand something gets to a critical level, people just turn off. Than level isn't very high.

      People can understand getting to the moon, they will never understand what a Gaugino is or will they care. Particle physics has no popular constituency.

      The take away, once particle physics is dead, it will never rise again.

    6. If particle physics is stopped it is possible it will not arise again. The comparison with flying astronauts to the moon is somewhat illustrative, in that the Apollo-Saturn program was worked out in 10 years, whereas trying to duplicate this effort now is taking longer and appears more difficult.

      As Peter indicates though it might revise with different methods. In particular the current approach to building particle accelerators is based on the idea Lawrence developed originally in the late 1930s to 1940s time period. The electric field oscillates in RF cavities to push a charged particle along. The electric field density can only be made so large. However, with a plasma you can get charge separations by optical means that have much larger field density. Other means might work as well, so we can increase the EM field density used to accelerate a particle by many orders of magnitude. In this way a putative 100TeV accelerator might be in a ring a kilometer in diameter instead of 60km as proposed with the FCC.

      It is the case that particle physics does not have the power appeal that large rockets do. Yet remember that particle physics got its early push due to the ultimate physics experiment conducted on July 16, 1945. Nuclear physics illustrated how the understanding of nuclei and particles lead to this enormous power. Of course there has not been much follow on of that sort with particle physics. The nuclear industry has stalled in ways, and the prospect of some new energy source seems remote. Maybe if we can push to higher energy we can find if the Higgs particle is a manifestation of the sphaleron. The sphaleron conserves baryon plus anti-lepton number and anti-baryon plus lepton number. As such this physics might it found permit us to directly convert matter to energy. That would be a game changer, though in the end the same sort of maniacs who got control of nuclear bombs will doubtless end up in control of this.

    7. The various forms of wakefield acceleration are interesting technologies that continue to be studied for decades. However the beam emittance, energy spread, top energy, beam intensity, duty cycle, operational lifetime, reliability etc. that can be achieved are, multiplied together, double-digit orders of magnitude worse than the requirements of a 100 TeV collider. These radically different approaches should be and continued to be studied of course, but one should not believe they will present a magical lower-cost technology that would make the 100 TeV range economically accessible compared to current accelerator designs.

      Even the FCC is at the limit of accessible realistic technology in the 30-40 year time span. The reason why the "current approach" is so very resilient is that it is actually extremely good.

  29. Optical telescopes offer an interesting analogy. The Palomar Observatory saw first light in 1949. The glass blank spent World War II cooling enough before it could be ground into a mirror. The Palomar was the largest optical telescope in the world (*) until the mid-1980s when new technologies, like the honeycomb active focus optics used in the Keck, were developed. Since then a number of monster optical telescopes have been built, but there was nearly a 40 year gap.

    The old technology, grind a huge glass blank that might take years to cool, had reached its limits. A new technology involving precision machining and computer controls was developed and augmented with advances in interferometry, laser guide star focusing and image processing.

    Starting in the 1930s, physicists developed more and more powerful particle accelerators that were basically the original frying pan sized cyclotron with higher magnetic fields, higher energies, other refinements and much improved sensors. The LHC is the Palomar reflector of the particle physics world.

    It's not as if no one did astronomy between 1949 and 1990. There were lots of big telescopes. There were all sorts of new bandwidths to explore. The universe offered a variety of surprises.

    You are absolutely right. Physics, even fundamental particle physics, could do a lot more with the money that would otherwise go to build a new LHC like collider.

    1. In our universe, only electrons and protons exist as stable particles that can be readily produced and artificially accelerated to the highest energies. They need to be accelerated in a vacuum to prevent them from colliding with air molecules. A magnetic field is needed to bend or focus the particles; an electric field is needed to accelerate the particles. The field should alternate at high frequency since this is the most efficient. Thus an accelerator becomes either circular or linear. This is not a matter of "more technology", it is a matter of principle.

      Other than these very basic principles, the 1930's cyclotrons and the superconducting LHC synchrotron have little in common.

  30. 20 billion dollars is nothing in big scale.

    Trump increased military budget by 60billion this year.
    Germany built an airport with 15billion and it doesnt even work.

    And no country is funding this alone either, but multiple countries.

    Your mindless witch-hunt against particle physics has no meaning and is entirely pointless.

  31. @Alex: Is that the best argument you can come up with? Out of the four top latest discoveries in high-energy physics, three have not come from large particle accelerators. (I'd say these four are neutrino mass, dark energy, gravity waves, and the Higgs particle. Feel free to criticize this list, but note that three of these have won Nobel prizes.) Why don't we put the 20 billion into gravity-wave detectors, neutrino experiments, and telescopes? Or at least ask the neutrino physicists, the gravity-wave scientists, and the astronomers whether they want some of the 20 billion? (Hint: I am absolutely sure they can probably spend all of it in worthwhile ways.)

  32. You really undermine the knowledge and technology thats has been developed while finding the Higgs (and top quark etc.)

    Multiple countries are building neutrino detectors.

    eLISA is still going on.

    Theres nothing to prevent a much better collider except mindless physicists who thinks money is an actual problem and not a marketing problem.

  33. Alex: Your assertion that we're not canceling projects because of money is blatantly false. Look at the wikipedia entry for the Overwhelmingly Large Telescope, which was canceled because a mere €1.5 billion was thought to be to expensive. You could a dozen of them for the cost of the next generation collider.

    Is the scientific value of the next collider twelve times as large as the scientific value of the Overwhelmingly Large telescope? Did anybody even think to do this comparison?


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