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| Image: CERN |
Since the late 1960s, when physicists hit on the “particle zoo” at nuclear energies, they always had a good reason to build a larger collider. That’s because their theories of elementary matter were incomplete. But now, with the Higgs-boson found in 2012, their theory – the “standard model of particle physics” – is complete. It’s done. There’s nothing missing. All Pokemon caught.
The Higgs was the last good prediction that particle physicists had. This prediction dates back to the 1960s and it was based on sound mathematics. In contrast to this, the current predictions for new particles at a larger collider – eg supersymmetric partner particles or dark matter particles – are not based on sound mathematics. These predictions are based on what is called an “argument from naturalness” and those arguments are little more than wishful thinking dressed in equations.
I have laid out my reasoning for why those predictions are no good in great detail in my book (and also in this little paper). But it does not matter whether you believe (or even understand) my arguments, you only have to look at the data to see that particle physicists’ predictions for physics beyond the standard model have, in fact, not worked for more than 30 years.
Fact is, particle physicists have predicted dark matter particles since the mid-1980s. None of those have been seen.
Fact is, particle physicists predicted grand unified theories starting also in the 1980s. To the extent that those can be ruled out, they have been ruled out.
Fact is, they predicted that supersymmetric particles and/or large additional dimensions of space should become observable at the LHC. According to those predictions, this should have happened already. It did not.
The important thing is now that those demonstrably flawed methods were the only reason to think the LHC should discover something fundamentally new besides the Higgs. With this method of prediction not working, there is now no reason to think that the LHC in its upcoming runs, or a next larger collider, will see anything besides the physics predicted by the already known theories.
Of course it may happen. I am not saying that I know a larger collider will not find something new. It is possible that we get lucky. I am simply saying that we currently have no prediction that indicates a larger collider would lead to a breakthrough. The standard model may well be it.
This situation is unprecedented in particle physics. The only reliable prediction we currently have for physics beyond the standard model is that we should eventually see effects of quantum gravity. But for that we would have to reach energies 13 orders of magnitude higher than what even the next collider would deliver. It’s way out of reach.
The only thing we can reliably say a next larger collider will do is measure more precisely the properties of the already known fundamental particles. That it may tell us something about dark matter, or dark energy, or the matter-antimatter symmetry is a hope, not a prediction.
Particle physicists had a good case to build the LHC with the prediction of the Higgs-boson. But with the Higgs found, the next larger collider has no good motivation. The year is 2019, not 1999.
"the “standard model of particle physics” – is complete. It’s done. There’s nothing missing."
ReplyDeleteExcept for neutrino masses...
"With this method of prediction not working"
Which method are you talking about?
Because so far you only described the chain: theoretical predictions -> experimental tests, i.e. the scientific method.
Are you proposing a different method?
Also, you seem to make a lot of confusion between the reasons behind a given theory (which may very well be not sound, flawed, you name it) and the actual mathematical content of the theory. You conflate these two into one single aspect and then you call the predictions "not based on sound mathematics" and "demonstrably flawed methods".
Well, that's just wrong, unless you want to claim that the theories themself (which, I'd like to remember, are simply extensions of the same quantum field theories that work in the Standard Model, not esoteric math stuff like string theory or quantum loop gravity) are flawed and not mathematically sound.
Claudio,
ReplyDeleteYes, that is right, I wrote about neutrinos here. But I hope we agree that there is no reason to think right-handed neutrinos should be anywhere below the Planck scale, and that a collider isn't the right experiment to test the Majorana case.
"With this method of prediction not working"
The method of prediction that I was referring to here specifically are arguments from naturalness. I said this very clearly. For the WIMP miracle you also us numerical coincidences more generally and grand unification is an argument from beauty. I explain the various different arguments in great detail in my book. The paper I mention is only about arguments from naturalness. For particle physics, those are currently the most relevant ones.
I did not say, not here and not elsewhere, that the theories are mathematically flawed. I do not know why you think I said something like that.
Neutrinos, yes. Fertile ground for particle physicists.
ReplyDeleteSo are dark matter searches; if it’s a particle, we have no idea what (maybe it’s a zoo of particles). So, look everywhere! Should keep particle physicists busy for at least a decade.
And all those apparent anomalies, who’s going to painstakingly investigate them,if not particle physicists?
"The method of prediction that I was referring to here specifically are arguments from naturalness"
ReplyDeleteOk, that was not so clear to me from the text.
Sabine,
ReplyDeleteDid you read any of the FCC Conceptual Design Report? I'd really recommend Volume 1 - Physics Opportunities: https://cds.cern.ch/record/2651294?ln=en. Your blog posts seem to suggest that all the arguments in favour of building a next generation collider are based on theories that we already know to have failed. But this is simply not true. Volume 1 of the CDR is a careful study of the present state of knowledge post the Higgs discovery, and - honestly - most of the physics opportunities identified are based on precision measurements of existing SM physics. Supersymmetry hardly gets a mention (it is referenced in a couple of pages in a 200+ page report) and then mostly in the context of the FCC as a 'discovery machine', able to rule out its 'predictions'. Yes, there are references to dark matter candidates, in Chapter 12, which is just 7 pages long, and neutrino masses in Chapter 13 (4 pages).
For me, the following passage provides the kind of context needed to judge these proposals properly (it appears on p. 7, under the section heading 'Unknown Unknowns':
"That no new particles beyond the Higgs have yet been found, or any significant deviations from theory was yet detected at the LHC, does not mean that the open questions introduced above have somehow evaporated. Rather, it shows any expectations for early discoveries beyond the SM at the LHC – often based on theoretical, and in some cases aesthetic, arguments – were misguided. In times like this, when theoretical guidance is called into question, experimental answers must be pursued as vigorously as possible. The combination of accelerators that are being considered for the FCC project offers, by their
synergies and complementarities, an extraordinary tool for investigating these questions."
Even within the context of the SM, particle physics didn't end with the discovery of the Higgs. To suggest that this is all a big waste of money because particle theorists haven't been able to get their act together is in my view equally misguided. Now - more than ever - we should put our trust in experimentalists to try to find a way forward.
Of course, arguments based on return on investment - that we might get better value investing the money in other areas of science - remain perfectly valid. And I'll be the first to admit that without an obvious search target, the FCC will be a much tougher sell.
Hi Sabine
ReplyDeleteCould you please comment on the assertion made here
https://ncatlab.org/nlab/show/flavour+anomaly
And whether it is in the category of flawed methods you mention.
Thank you,
Charles
Hi Sabine,
ReplyDeleteI learnt that hope and fear are the two sides of the same coin.
So, I would like to know if you see anyone shaking ?
Best,
J.
(..and nice post, btw).
Jim,
ReplyDeleteAs I said various times before I read parts of it. I hope those were the relevant parts. I also read the summaries.
"Your blog posts seem to suggest that all the arguments in favour of building a next generation collider are based on theories that we already know to have failed."
Huh? This is totally not what I am saying. I am saying that the only good arguments in favor of building the next collider are based on the only theory we know that works, which is the standard model. There are no other good predictions besides that.
In case you are referring to various anomalies. Sure, if one of them holds up, that would make a strong case. But I suggest someone should quantify the probability of there being so-and-so many anomalies at any time in the data before getting too excited.
Charles,
ReplyDeleteAn anomaly is not a method. I don't understand the question, sorry.
akidbelle,
ReplyDeleteNot sure what you mean. Are physicists worried that there will be no fundamentally new particles to find at the LHC now? They surely are. I have documented this in my book. Are they worried that the next larger collider will not get funded? I don't think so. They seem very confident, illustrated, eg, by their unwillingness to think about what to do in case the next larger collider will not come to pass.
Thanks for the kind words. Best,
B.
There's also the immense opportunity cost to consider--it's a terrible waste that we encourage so many smart people to pour their careers down a rat hole.
ReplyDeletePhil Hobbs
Sabine,
ReplyDeletePerhaps I misinterpreted your comments:
"Fact is, particle physicists have predicted dark matter particles since the mid-1980s. None of those have been seen."
"Fact is, particle physicists predicted grand unified theories starting also in the 1980s. To the extent that those can be ruled out, they have been ruled out."
"Fact is, they predicted that supersymmetric particles and/or large additional dimensions of space should become observable at the LHC. According to those predictions, this should have happened already. It did not."
I suspect the problem here is the belief that "beyond SM physics" must mean some radically new physics that blows the SM apart and involves a new smorgasbord of particles. But it's much more likely that going beyond the SM will require a detailed study of what we think we already know about it. As far as I can tell, the principal justification for the FCC is to do just this, with the added benefit that IF there are indeed any new particles or phenomena to be discovered that are not consistent with what we think we already know about the SM, the FCC will find them.
This isn't about travelling hopefully - this is science doing what science does, which is to look more closely at things that we think are already familiar. Yes, the gains might well be incremental rather than paradigm-shifting and yes, there's a risk that such gains in knowledge might not justify the price tag. But that's a different argument.
@ Phil H
ReplyDeleteAs I like to put it: for some tunnel visions there is no cure.
"All Pokemon Caught." Literally LOL.
ReplyDeleteElliptic, plane, and hyperbolic geometries each exclude the others. Theory disputing theory absent Popper is noise. Physics demands "accepted theory," ending evolution.
ReplyDeleteSparse matrices demand exact vacuum symmetries. Group Theory is rigorous, then Emily Noether. Exact vacuum symmetries toward hadrons (quarks): gravitation does not quantize, Tully-Fisher lacks empirical source, SUSY mocks Popper, a post-Big Bang net matter universe is forbidden.
~0.1 ppb vacuum chiral anisotropy selective to hadrons heals all ills - but fills matrices. Two published experiments instead running crafted molecules empirically falsify QM and GR for a very selective footnote excluded by "accepted theory." 400 TeV accelerators? 0.001 eV dings all but QM, that requiring ~2 eV. Look.
Sterile? Lunch money lost. Fruitful? A whole science blooms. Look.
Field tech, "This fingerprint solves the case!"
ReplyDeleteInspector, "Suppose there were no fingerprint."
Field tech,"We'd be on this forever."
Inspector, "Lose the fingerprint."
Jim quoted: "... Rather, it shows any expectations for early discoveries beyond the SM at the LHC – often based on theoretical, and in some cases aesthetic, arguments – were misguided. In times like this, when theoretical guidance is called into question, experimental answers must be pursued as vigorously as possible. "
ReplyDeleteThat is a very good quote. I like it. Realist, truthful, optimistic. One can bring up whether the cost is justified unless there are reasons to think that the results are worth that much. If someone is on the side of challenging the justification, that's OK, too. (Even if they are a bit snarky at times.)
One read the quotes from the "superstars" of theoretical physics over the years where they were certain that susy was the answer, or wimps, or something else. There were enough of these quotes that were filled with arrogance and conceit to make me suspect. And then when someone points out to them that it didn't work out and "what do say to that?", the questioner get attacked and/or belittled. That "ad hominem" behavior is hurting the rest of the community where most people are reasonable and willing to debate politely.
Sabine said: "Their unwillingness to think about what to do in case the next larger collider will not come to pass."
I don't blame someone who is enthusiastic about something to also be an optimist -- at least in public. The critics cannot be expected to be found in the team that is making the proposals to fund something. I think Jim, by quoting the material he did, pointed out that this proposal is well considered.
Phil H.: ...so many smart people to pour their careers down a rat hole.
Tell me about it. I was a nuclear engineer. I can mathematically justify a 100000 year waste repository. Eventually, I realized that other people cannot.
Jim,
ReplyDelete"I suspect the problem here is the belief that "beyond SM physics" must mean some radically new physics that blows the SM apart and involves a new smorgasbord of particles."
We know that the standard model works very well at the energies we have tested so far and that will remain the case even if we find something new. Thus, the SM will certainly not be "blown apart".
"But it's much more likely that going beyond the SM will require a detailed study of what we think we already know about it. As far as I can tell, the principal justification for the FCC is to do just this, with the added benefit that IF there are indeed any new particles or phenomena to be discovered that are not consistent with what we think we already know about the SM, the FCC will find them."
I am telling you that there is no reason to think there is anything to be discovered that is not consisten with the SM and hence your "IF" does not make for a good justification.
I like your comment on the need for a sound mathematical derivation.
ReplyDeleteHi again,
ReplyDeleteSorry my question was not clear.
Urs seems to be arguing in
https://ncatlab.org/nlab/show/flavour+anomaly
further expanded in this paper:
http://cdsweb.cern.ch/record/2634813/files/dordei_nufact.pdf
that the presence of the anomaly is good reason to to pursue higher energy experiments at LHC2.
I was trying to understand if you thought that this phenomena was reason to support LHC2 or not.
Thanks again,
Charles
Great overview of the problem, Dr. H. I can't help but compare it to the Old and New Testaments, which are immutably fixed in stone. There are no new, rich verses in Isaiah, for example, pointing to fantastic new discoveries that will propel religious faith forward. And I long ago began to look upon string theory and SUSY as modern variants of religious belief.
ReplyDeleteSabine,
ReplyDeleteSorry but I really don’t understand your argument. Are you saying that because there’s no theoretical reason to think there is anything to be discovered, we shouldn’t bother to look? So when better microwave technology became available during and shortly after the war, nobody should have been bothered to look more closely at the spectrum of hydrogen, since theory already provided an adequate description? But then we wouldn’t have known about the Lamb shift, or that the g-factor of the electron is slightly larger than 2. These things were not predicted by any theory, yet their experimental discovery led to QED and, eventually, the SM.
I appreciate that the price tag is rather bigger, and there may be better uses for the money, but I really don’t think “there is no reason to think there is anything to be discovered” is a valid argument. And, btw, my IF related to an added benefit of the FCC, not my principal justification.
Sabine,
ReplyDeleteI share your concerns regarding expectations guided by arguments of beauty or naturalness - anyway rather subjective criteria. But I don't see, that a future collider would or could only be driven by such arguments - conceding, they might lead the public astray.
First of all a future collider is an experimental endeavor and should be judged from that perspective. I can well understand, that experimentalists strive to secure continuation of projects in their field. This will be important to secure and further develop much of the experience and capabilities in the field, which might be hard to regain when lost. Of course these projects need to make sense.
For the latter you stress the point, that there are no anyhow reliable predictions on which would provide a basis for this - different from the comfortable situation of the past decades. Theory is no easy guidance anymore. But I regard the statement 'with the Higgs found, the next larger collider has no good motivation' too strong. Should Physics abandon all research and leave it with the theories we have - well founded in the areas we have explored, though known to be not really complete?
The situation is perhaps similar to that before the dawn of the current particle physics, where exploration of uncharted territory with open mind but w/o many hints was needed. But luck alone will not be sufficient to proceed.
Your assumption, that only at the Planck scale new Physics can be expected is in a certain way also an argument of beauty - of the standard model and GR (you admitted, that anyway something may be found).
Obviously we simply have to live with not yet knowing, what occurs between some TeV and the Planck scale, so surely modesty is appropriate.
Whether the proposed infrastructure heavy collider is the best option in such a situation, is another question. I would rather advocate improved magnet technology, plasma / wake field acceleration and the like, perhaps colliding myons. Precision may be key to unravel small deviations from the standard model.
I have been doing some estimates, which I may write more about later. From my estimates, current discovery machines which arguably have a better motivation than the FCC or ILC have price tags of 1-3 billion USD (DUNE/HyperK/LIGO/AMS/LISA). The LHC (Higgs) cost more around 15 billion USD (without including all R&D) and the total price tag will be over 30 billion USD. I expect the FCC to be more (10 billion USD is surely an underestimate based on the costs of the LHC (Higgs)). That suggests that colliders (in the US/Europe) cost an order of magnitude over comparable discovery machines.
ReplyDeleteI think at this point (the one detailed by Sabine in her book) the right thing to do with money at this point is to fund a whole slew of students and physicists to work on whiteboards. Or computers. Physics may be at the point of chemistry, at this point, the things to look for are not new elements, but how the elements combine and interact. I know my folks (CS people) are busy simulating QM interactions on the world's fastest supercomputers, we can do an awful lot of that with $10B.
ReplyDeleteSo start beating the SM until you find cracks. In simulations, we can change some parameters until we match anomalies. Work on LQG. Find something that an experiment for a few million could reveal or settle or at least put some limits on.
Figure out how to do Penrose's test to see if there is a mass limit to quantum superposition; I've read recently that if there is one it is millions of atoms. Or can gravity or quantum foam cause spontaneous wavefunction collapse?
There must be other computations and theory work that could be done within the SM. If SM is complete but insufficient, and hardware experiments don't look promising, numerical experiments and exploration are what's left. I'd stop betting everything on one experiment, and bet it on ten thousand experiments. Do it like evolution, you only need one in a thousand ideas to be turn out to be a really good idea.
Say what you want about the necessity for a new Collider however, there's no denying those pictures of the LHC look so cool!
ReplyDeleteSabine,
ReplyDeleteThis seems like a remake of the post of a couple of days ago. While you are not changing musing, this time I will try change my strategy and try with a couple of more punctual comments (hopefully):
1) You write "Fact is, particle physicists have predicted dark matter particles since the mid-1980s. None of those have been seen."
This is kind of misleading, not to say not true. I think the only people who predicted dark matter are astrophysicists/cosmologists/GR people who, trusting GR (or even Newton gravity), had necessarily to come to that conclusion, because it is the simplest, I guess. Once this prediction was made (which might of course be wrong), I guess it is the most natural thing to do to try to look for it in the form of something that we understand, namely particles... I guess it would be stupid to do otherwise and not even try, wouldn't it? So I really don't know what your problem is.
2) You write "I am simply saying that we currently have no prediction that indicates a larger collider would lead to a breakthrough. The standard model may well be it. This situation is unprecedented in particle physics. "
Mmm, I would tend to consider this also as misleading or tending to false. Before the concept of "particle physics" and with it "collider physics" even existed, we barely knew what an electron was, definitely had no idea about quarks, other leptons etc. Even the concept itself of antiparticle was developed (almost) at the same time. Dirac wrote his equation in 1928, the positron was discovered (practically independently) in 1932. The connection was made afterwards, Anderson was not searching it, as far as I know. He was just curious and looked where he could look to see what there was. Period. Them people kept digging (without any sound mathematical reason, as Quantum Field theory itself did not exists as we know it today), built colliders, studied DIS processes, discovered quarks inside protons etc etc. If someone had done your crusade at that time, we would probably still believe that protons are elementary and would be looking for a theory of the strong interactions. It does not look like an nice outcome to me.
3) "The only thing we can reliably say a next larger collider will do is measure more precisely the properties of the already known fundamental particles. That it may tell us something about dark matter, or dark energy, or the matter-antimatter symmetry is a hope, not a prediction. "
Mmm. Right. And how is this not actually a great reason to build the next collider? Given the current situation, don't we need to do exactly that? On top of that, for how we understand physics today, this would be the ONLY way to study in detail the SSB mechanism. We have seen the Higgs, true, but we have no idea whether the Higgs gives masses to particles as we think our (very silly, I would say) phi^4 toy-model predicts. It is the first time we see an elementary scalar field, and this field turns out to have to provide all other fields with masses, in order for the Standard Model to be consistent. And we have NO IDEA whether this is the case. All pokemons have definitely not been caught, according to me.
As I said already, if you are happy with that, it is ok. But please, don't expect that we should all be.
Best
Lorenzo
Sabine, what is wrong with measuring SM Higgs sector to higher degree of accuracy?
ReplyDeleteBack in the days physicists measured X-ray emission lines, one thesis per line or few, to high accuracy. Only then we managed to find new theories.
LEP has not discovered anything, it "only" measured SM EW sector. Was LEP a bad investment?
Long time lurker here and a former professional Higgs Boson hunter...
ReplyDeleteIMNSHO the only justifiable new collider at present is a Higgs factory with the immediate future belonging to high precision tests of the Standard Model.
Last I looked the only oddities in the SM not related to the neutrino sector are in loop mediated B meson decays and possible violations of lepton universality in B meson semi-leptonic decays. Not sure what the prospects are for improving those measurements in the near term.
If I was to come up a list experiments to push to the limit they would include searching for forbidden processes such as:
K_L -> mu e
K+ -> pi+ mu e
B_s,d -> mu tau, e tau, e mu
mu -> e gamma, 3e
proton decay (possibly the most successful failed experiment in particle physics)
electron EDM
neutrinoless double beta decay
Once, if(?), any of these processes are observed, we will then have a clue as to relevant mass scale of the new physics
Allowed processes that need to be measure as precisely as possible (likely systematics limited at the LHC)
H0 -> gamma Z (possibly the most sensitive process to new physics in the Higgs sector)
H0 -> mu mu
Ain't ever gonna happen but I would love to see limits on t -> c H0
Higgs self coupling (find out what size and shape the sombrero really is)
BTW, I "predicted" years ago that M_H^2 ~ 1/2 m_t^2 which as far as I can tell was better than any SUSY based prediction...
All that being said, Particle physics as I knew it is now dead....
Me again, almost forgot g-2 for mu and tau....
ReplyDeleteNot holding my breath for the tau though...
Bee
ReplyDeletePeter Woit's blog lists the several options, of these, the HE-LHC using 16 tesla magnets and ~28 TEV pp collisions represent the least expensive upgrade path at ~$7 billion since everything else can be reused, and soonest
maybe some nation might also invest in a linear e-e- collider or even china building the 100TEV collider.
its possible CERN won't have the money to spend $10 billion for FCC-ee then another $17 billion for the FCC-hh
if this HE-LHC doesn't find SUSY, then that would further strengthen your argument against naturalness with actual data, as some SUSY theorists like Gordon Kane now claims gluino masses are above LHC energies, and can still satisfy naturalness.
But we can always party like it's 1999, can't we?
ReplyDeleteDr. Hossenfelder, what do you consider “not consistent with the SM” to be? That’s a bit vague.
ReplyDeleteCharles,
ReplyDeleteMy blogpost is commenting on the planned new collider FCC. The LHC run 2 is done already. The planned high luminosity upgrade is currently being done. I don't understand what you are asking.
M_Malenfant,
ReplyDeleteThe purpose of my blogpost is to clarify the situation. Of course people who are fond of particle physics, including particle physicists, would (will) say that probing the standard model more precisely is sufficient motivation. I have no problem with this argument. I just wish they would not overstate the potential for new discoveries.
What you say about the Planck scale is not correct. We know that quantum gravitational corrections will become relevant eventually, and we know that it's not consistent to just leave gravity quantized. It is a prediction of similar logic as that for the Higgs: We know that at the Planck scale something new must happen. Math alone cannot tell us just what, but we know something has to be there. The same kind of logic does not underlie arguments from naturalness.
(I explain this in my book, btw.)
Jim,
ReplyDeleteAs you note the price-tag is high. This means we have to be careful what to invest the money in. I merely point out what particle physicists are well aware of, but often forget to mention: that there are no good reasons to think this money will deliver something new.
Willingness to take risks is a value decision and it differs from one person to the next. Maybe I am more risk averse than you are. But really this doesn't matter because it's not a decision that will be made by you and I. I just want to make sure that the people who will make the decision have all the relevant information.
Regarding your example. Certainly you know that if you take mathematical consistency seriously, then the need to make quantum mechanics relativistic plus knowing classical electrodynamics will eventually lead you to QED and render the findings you mention predictions. Ie, even if you had not made the investment without the prediction, you'd still eventually have gotten there. What I am saying is that when an experiment is as expensive as the FCC, and you have to chose what's the best way forward, you should look in those places that are most promising to lead to breakthroughs first. This is presently not the case for high energy particle collisions.
Lorenzo,
ReplyDelete1) I am referring here specifically to supersymmetric particles and axions as dark matter candidates. Those have been searched for in direct detection experiments starting in the 1980s. As I am sure you know, the range in which those particles were supposedly to be found has moved whenever there has been a null-result and is now more than a factor 100,000 beyond the original range. Particle physicists have never had a shortage of models for that. This is all well-documented in the literature.
2) As you note yourself, you are referring to a time when there wasn't even such a thing as particle physics. Thus, I do not know what you think is misleading about my statement. I state in my blogpost explicitly that I am referring to the time past the particle zoo in the 60s.
More generally, the argument "just let curiosity lead the way" is all well and fine and I certainly wish we could do that. We cannot. Experiments have become too large and too expensive. You don't just build $20 billion dollar machines because some experimentalists would like to play with it. Those days are beyond us. We have to think carefully about what to invest in now.
3) As I said many times before, if you think that measuring more precisely the properties of standard model particles is sufficiently good motivation to invest in the FCC, that's all fine with me. I merely want people to understand there is no reason such a machine would see anything new.
Maly,
ReplyDeleteI am not saying there is anything wrong with this. I am just saying that if you want to make new breakthroughs it's not a particularly promising avenue to continue.
Regarding LEP, we have known since the 70s that CP violation requires a 3rd generation. LEP therefore had a very good motivation. That they'd eventually be beaten to the discovery of the top by Fermilab doesn't negate the motivation.
neo,
ReplyDeleteYes, of course, as I have stressed, what I say is an assessment from the present state of knowledge. If the LHC goes on to find SUSY that would entirely change the situation. In that case I'd have no doubt a next larger collider would be built, maybe even two.
I hadn't heard that Kane now claims gluino masses are above the LHC range. Last time I looked, he had moved them out of run 1 and was arguing they should be in run 2. I have noticed, though, that Howard Bear claimed already in 2016 susy should be to find at a next generation collider and not at the LHC. You have to give the man credit for being forward-thinking. In any case, excuse my cynicism, but why does anyone still believe what these people "predict"?
Tanner,
ReplyDeleteI mean any observation that cannot be explained by the standard model.
Sabine
ReplyDelete"the argument "just let curiosity lead the way" ... We have to think carefully about what to invest in now."
This really looks like an "innovation's killer" argument.
In which fields (evt. outside physics) or experiments do you think it is worth to invest ?
CM,
ReplyDeleteWe should focus on those cases where we have an inconsistency, either between theory and experiment or an internal inconsistency in the theory. Right now this means concretely dark matter, quantum gravity and quantum foundations. I explained my reasoning in brief here and further details are in my book.
If you are asking outside the foundations of physics, I'd put more money into nuclear fusion research. We know that nuclear fusion works and the potential benefit is enormous, so I think it's a case where the costs are justified. If you are asking outside of physics, I am not competent to comment.
@Sabine
ReplyDelete"You don't just build $20 billion dollar machines because some experimentalists would like to play with it."
To put this number in perspective, you could almost build a wall along the southern border of the USA for that money:
https://www.foxnews.com/opinion/trumps-border-wall-how-much-it-will-actually-cost-according-to-a-statistician
Sabine,
ReplyDeleteThank you for your answer. I appreciate.
You seem to complain that there is a lack of data in physics, that physicists are “lost in Math”, and you propose even more mathematical research on the "foundations of physics".
Moreover, the “foundations of physics" does not need many investments. A researcher with a blackboard and some colleagues is ok.
Fusion: There a allready projects in this field.
CM,
ReplyDeleteWe do not have a lack of data. We have loads of data. It's just that that data doesn't contain evidence of any phenomenon that's not explained by the existing theories. (Except for dark matter.) Yes, I know there are already projects on fusion power.
Hi Sabine,
ReplyDeletesince all of this eventually relies on experimental data, would you know the status of the muon g-2? There is already a nice discrepancy at 3-3.5 sigma, and I think there should be new experimental data in the pipes right now. Right?
I also heard there is now a 'double' anomaly, which I do not understand. Please could you explain or point me to a readable paper (or to an older post maybe).
Best,
J.
Hi akidbelle,
ReplyDeleteYes, it's currently at 3.7 sigma and Fermilab's J-PARC is expected to deliver new results later this year. I don't know what "double anomaly" refers to, sorry, maybe someone else knows.
Sabine,
ReplyDeleteJust for fun.
Lord Kelvin: "Radio has no future"
The only thing you could have written to cause more outrage than this would have been to write "Perhaps dark matter isn't a particle at all. Maybe it doesn't even exist." ;)
ReplyDeleteThe Antarctic Impulsive Transient Antenna (ANITA) experiments indicate signals suggestive of the s-tau at around 10^6 TeV. This is also at the upper limit for cosmic ray energy. If this is to found to be a signature of SUSY, where this is being hammered out, we then have accomplished that goal. This energy is four orders of magnitude above what this FCC can achieve.
ReplyDeleteLawrence,
ReplyDeleteIt's two events. This isn't enough data to make reliable statements about what it is.
Does the fact that the effective field theory that is the Standard Model is perturbatively renormalizable tell us anything other than that amount by which non-renormalizable terms are suppressed suggests that new physics is to be found only at a very high energy scale?
ReplyDeleteArun,
ReplyDeleteNo, but it tells you that you don't need new physics because the SM is fine as it is. (Up to the Landau Pole that is, but that's even beyond the Planck scale.) There are many ways to add new particles without ruining renormalizability.
Sabine,
ReplyDeletethank you for the reply.
It seems I have written misleadingly: I know that corrections are expected at the Planck scale, my point was, that expecting explicitly nothing below it because SM and GR don't predict it appears to be a kind of (negative) beauty argument. This would be a big desert with nothing to be found in it. But of course, that is no real argument and cannot be excluded.
The point will be, how to proceed most effectively with limited budgets without unjustified expectations but still work to find new indications.
M_Malenfant,
ReplyDeleteI didn't say I expect nothing below the Planck scale. I said we have no reason to expect something. At least not at present. Situation may change every day.
@Bee: I agree two data points is not a lot to hang a hat on. However, the stats on these data points is very good. In time we might have more to work with.
ReplyDeleteWe in the west have a lot of strength by being impatient. It is also are biggest weakness.
Lawrence,
ReplyDeleteI think you misunderstand my point. I am not saying the stats of the two data points are not good (they look very reliable, at least to me), but that from those you can't make proclamations about what it is. It's just not enough information to pin down a model.
Sir Edmund Hillary when asked why he climbed Mt. Everest is quoted as answering,"because its there." Taking all the scientific arguments aside and all the alternatives money could be spent on like helping the poor, what would be the reason for building the next collider? Because we can. What if Columbus never sailed west to the new world? What if Marco Polo never went to China? What if there was no declaration of Indepedence or a Constitution? All these were bold adventures into the unkown. We don't need a reason to build an FCC other than that for the adventure of discovery itself. Besides, in this increasing world of femininity and female empowerment a new high testosterone toy would be a welcome thing for the male gender.
ReplyDeleteChris,
ReplyDeleteArguing that we should build something because "we can" is not very helpful if you have to decide what to build. We can, presumably, build an artificial mountain higher than Mt Everest. But is this something we should do? I don't think so.
Hi Sabine, it seems to me like astroparticle physics (b_mode polarization included) and the emerging field of gravitational wave astronomy would be a good place to invest more money (versus colliders) as it seems very promising for even fundamental physics . Since we know there must be BTSM physics in quantum gravity. What are your thoughts on that direction for experimental physics s?
ReplyDeleteSabine,
ReplyDelete"We know that nuclear fusion works and the potential benefit is enormous, so I think it's a case where the costs are justified."
Besides the thermonuclear explosion what else we know that fusion works ? (I guess you mean that the work is the gain of energy in the experiments, not theoretical conclusion.)
Best
Valeriy Tarasov
"...a new high testosterone toy would be a welcome thing for the male gender"
ReplyDeleteThe CERN director is Fabiola Gianotti
This comment has been removed by the author.
Delete@Mogens: "The CERN director is Fabiola Gianotti"
Delete*rimshot* [caused by a torrent of particles sailing through a double-slit barrier and hitting a screen]
VYT,
ReplyDelete? I am afraid I don't understand the question. Physicists have done nuclear fusion countless times in controlled environments. It's just that we normally put more energy in than we get out. It's a technological problem, but a solvable one.
Sabine,
ReplyDelete"It's just that we normally put more energy in than we get out."
Exactly.
"the potential benefit" of nuclear fusion you have mentioned is energy generation
from the fusion reaction - 2 1D + 3 1T → 4 2He + n0 (what is expected to happen in ITER).
The energy gain from this fusion reaction was never shown experimentally, so we dont know if that
nuclear fusion works. Only theory justify this reaction, its "the potential benefit". Am I wrong ?
Best
Valeriy Tarasov
Fusion is interesting, as it's also an illustration of groupthink leading to a dead end, albeit a technological and economic rather than scientific one. Fusion is likely to "work" in the sense that a machine can be built that generates net power, but it has long been clear it's unlikely to ever be competitive or practical (and this conclusion has only become more strongly justified over time). As such, funding for it is as difficult to justify as ever larger accelerators would be.
ReplyDeleteFor all we know, particle physics may be like trying to learn atomic physics by studying atoms at ever higher temperatures, and somehow thinking that if 10, 100, 100, and 1000 K produced results, then 1000 000 K should also reveal something. At some point, it's just a mess. The thing is we don't and can't _know this_ for sure. But it seems there are better places to look for physics with 25 billion $.
ReplyDeleteRegarding your op-ed on particle physics in the New York Times, it's my feeble understanding of particle physics that smacking particles together simply makes new particles, though maybe the Higgs boson is the completion of the particle discoveries achievable with current technology.
ReplyDeleteDiscoveries aren't necessarily made with hugely expensive equipment, just sharp observation that leads to a line of inquiry. One of my thoughts about dark matter has to do with quarks. Why should one assume that all of the quarks flying around in the Big Bang latched together to make common particles? What if a large number of quarks didn't bump into other quarks to make particles and continued to float around as free quarks, mass that maybe doesn't have normal interaction with electromagnetic radiation and appears as dark matter? Might those quarks eventually condense into normal matter and then form new stars, etc?
Or what can one say about time-dependent quantum mechanics that might explain foreshadowing or echoing of significant events? Or what is the role of information in the world? Can reality be manufactured by information aka words? What connections are there between physics and life? Is life more than just a specialized form of oxidation-reduction reaction, just a kind of fire?
There's a piece by a new opinion writer featured close to the top of today's online New York Times. Here's a screen capture:
ReplyDeletehttps://drive.google.com/file/d/1Tpf4szMHS1rkK2w7J6DWVphmTuKl2fyU/view?usp=sharing
Great article! Congratulations!!!
We'll build an accelerator ring around Earth, and then the Sun. Quantum gravity deserves the test.
ReplyDelete@everyone
ReplyDeletei just want to call attention to the opinion piece by bee in the New York Times today(1/24/19). i think it's behind a paywall (i'm not sure since i have a subscription) but perhaps someone can make it available to everyone;
naive theorist
Sabine,
ReplyDeleteOh, I really, really wish you hadn’t made this argument. You seem to be dismissing experiment as almost irrelevant, as the theorists would have gotten to QED in the end.
I’m sorry, but this is not how science works. At the time of the Shelter Island conference in 1947, theoretical physics was in crisis. The theorists had a quantum field theory but couldn’t get past all the infinities that plagued it. It was hearing about new measurements directly from Lamb and Rabi that made them realise that the corrections needed were finite. Following a suggestion, on the train back to Schenectady Bethe invented renormalisation.
The thing about experimental data is that they really help to focus the minds of those theorists ‘Lost in Math’, as you would have it.
Sabine,
ReplyDeleteRegarding LEP, we have known since the 70s that CP violation requires a 3rd generation. LEP therefore had a very good motivation. That they'd eventually be beaten to the discovery of the top by Fermilab doesn't negate the motivation.
Are you saying here, that LEP was built to find the top quark, and that it was unsuccessful because it was beaten by the Tevatron? If so, that is surely an unconventional interpretation of history. And would, again if I read it correctly, bear witness to a sensationalist view on physics where only discoveries of new particles and/or phenomena count.
I assume you are aware that the LEP precision measurements confirmed the quantum structure of the Standard Model as developed by t’Hooft and Veltman. And that exactly the quantum loop effects allowed LEP to determine the top quark mass to an impressive precision of 173 +13 - 12 GeV *before* it was eventually seen at the Tevatron exactly where LEP had pointed to it. So, LEP was certainly not beaten by the Tevatron. On the contrary, the Tevatron helped to underline the success of LEP.
Also you are certainly aware that LEP determined that there are three neutrino species in nature.
Best,
Mogens
Mainstream high energy physics rests on two approaches: either build a bigger machine and hope that something new shows up or follow the precision approach where one hopes that some (small, but relevant) discrepancies show up. Typical examples are the new super-collider, on one hand, and the g-2 experiment, on the other.
ReplyDeleteI am wondering why so little is said -- also in this blog -- about neutrino physics. After all, the only evidence for physics beyond the standard model that has shown up so far is the discovery of neutrino oscillations and the consequence that neutrinos have mass. That was achieved in an experiment without a new accelerator and with beams of neutrinos whose energy was not even known to any 'normal' precision. And at the same time the solar neutrino problem was solved!
The only predictions we have left are quantum gravity and maybe the [a href="https://en.wikipedia.org/wiki/Seesaw_mechanism"]seesaw mechansim[/a]
ReplyDeletethat predicts massive right-handed neutrinos. Both of these are experimentally far out of reach.
At least one particle physicist I've talked to (before the LHC started operating) thought the see-saw mechanism was much more likely than supersymmetry or large extra dimensions. So why did we never hear about it. I would guess because it didn't predict anything that would be observed by the LHC.
Of course, you might could also consider the seesaw meechanism an argument from naturalness, so maybe your reasoning works against it as well,
"The energy gain from this fusion reaction was never shown experimentally, so we dont know if that nuclear fusion works. Only theory justify this reaction, its "the potential benefit". Am I wrong ?"
ReplyDeleteYes. Starts are powered by nuclear energy. We know that that works, and how, in detail.
The CMS collaboration has a new bump a 28 GeV. They're already saying "new physics?"!
ReplyDeleteIt is about time that modern physis will rediscover that eventually, "there is no spoon," or, by the way of Meister Ekhart:
ReplyDelete"[...]your own are burning and your memories and you don't want to leave them. Everything will burn to the end, you suffer, but nobody is punishing you, they are just setting your soul free. Don't be afraid because while you fear death they will rend your soul like demons. Only calm down and you will see the angels who are setting you free, and then you will be free."
Jim,
ReplyDeleteLook, I just wrote a post only a few days ago in which I wrote explicitly that breakthroughs come in two types, either experiment-led or theory-led. Clearly, I am not dismissing experiment as "almost irrelevant". The whole point of my book is to point out that without data (that is not explained by the already existing theories), theory-development runs a high risk of getting stuck.
"The thing about experimental data is that they really help to focus the minds of those theorists ‘Lost in Math’, as you would have it."
So if the FCC goes and confirms the standard model at even higher energies, how do you think this is going to help those theorists? The only thing they learned from the LHC is to move their predictions to even higher energies. Enough of that, is what I say.
Quant,
ReplyDeleteYes, neutrino physics is great, I love neutrinos. Look, I cannot cover every topic in every blogpost. I wrote about neutrinos here and here and here to mention a few instances.
Better screenshot of today's New York Times:
ReplyDeletehttps://drive.google.com/open?id=1oPx_61NxH8Ynrfouk8Z6WXk4gz7fqprN
"The only reliable prediction we currently have for physics beyond the standard model is that we should eventually see effects of quantum gravity. But for that we would have to reach energies 13 orders of magnitude higher than what even the next collider would deliver."
ReplyDeleteAhh so Sabine wants a really, really big collider ;)
I remember talking to a friend twenty years ago who was studying post graduate physics. He said then that the GUT theories he was working on would require an accelerator the size of the solar system to test. Not much has changed.
Sabine's argument that a future collider does not look like good value for money makes a lot of sense. We could fund many more targeted experiments to look at known anomalies to try to pin down particle physic's future direction.
I guess part of the problem is that a large collider like this is a great prestige project. Bringing together thousands of physicists from across the world, meeting at the World's particle physics hub. Other projects don't have that allure.
@Phillip Helbig
ReplyDelete"Yes. Starts are powered by nuclear energy. We know that that works, and how, in detail."
?! There is obvious difference between astronomical observations and data from controlled experiments. You cannot do an experiment with stars and you cannot say that the fusion reaction I have mentioned has experimental confirmation from any astronomical observations.
A theory based on the astronomical observations is far less reliable and more speculative than any theory based on experiments (of course the controlled experiments, since an experiment without controls is nonsense in science). Again, the star argument is a theoretical argument, not an experimental one.
BTW, about controls in science.
Your argument (in the post earlier) against the performing the following SM control - the collision of two electron beams to confirm electron-positron pairs generation :
“No, the SM is not under question or in trouble because this experiment hasn't yet been performed.
The standard model also says that the cross section for various interactions doesn't depend on the day of the week, or how many people are in London at the moment, or whatever. I believe them, despite the lack of control experiments.”
I cannot take it seriously since the control I have asked about is a consequence of SM. But, the people in London and the cross section for various interactions are not related to each to other.
BTW, In USSR the collider for the collision of two electron beams existed (1963 - 1968) and didn't show any pairs generation, but the energy was relatively low - up to 160 МэВ. (info only in Russian - https://ru.wikipedia.org/wiki/ВЭП-1)
Sabine,
ReplyDeleteThis will be my last comment (relief all round).
I think you’re still missing the point. Of course there is a risk that the FCC will yield results all in perfect harmony with the SM, and we don’t move any further forward. But I chose my historical example quite carefully. More precise measurements on the H-atom spectrum - which was thought to be entirely consistent with theory at the time - revealed small inconsistencies. These helped to point the theorists in the right direction, and the result was QED.
Nobody knows what will be revealed if we make more precise measurements of what we think we already know from the SM. But if there’s a chance we might find some more small inconsistencies, I believe we should take it, if only to try to end 40 years of pointless fairy-tale physics.
Yes, the price tag is high. But the SSC was canned by congress in 1993 because a single nation - even one as big as the US - couldn’t afford to find $11 billion AND the $25 billion needed to build the International Space Station. CERN is in contrast a multinational, collaborative effort which helps to spread the cost.
Sabine, "Clearly, I am not dismissing experiment as "almost irrelevant." Politely and gently, you are. 400,000 theorist years' 3 million published pages are empirically sterile. Fruitful future observations must contradict accepted theory but not documented observation. They are actively excluded for being "wrong."
ReplyDeleteChemistry offers 0.001 eV rotational spectroscopy (SUSY, dark matter, cosmological constant, GR versus baryogenesis) and ~2 eV diffraction times interference (QM versus Hundt's paradox). EM combs offer ultra-high resolution frequency counting (DOI:10.1126/science.aav2616).
Observations are ready. Shoot armor piercing rounds, not blanks.
I wonder if we are doing a disservice thinking about this from the public’s perspective or from the perspective of advancing fundamental physics and instead should think about this from the perspective of the funding agencies. I think that there is a good case that they care primarily about patents, Nobel Prizes and publications/citations.
ReplyDeleteBasic science isn’t where you get the most bang for the buck from patents and Nobel Prizes are closely related to advancing our understanding of fundamental physics (and so there are probably other better per dollar investments), but citations are a bit independent of significant discoveries and colliders do much better per dollar there than many other Discovery machines.
It is probably the case that from a funding agency perspective a new collider makes sense, unless there is significant push back from the public or scientific community.
I do not have a subscription to the NYT, I was able to access and read the article by it's title;
ReplyDeleteG("The Uncertain Future of Particle Physics"), it is the second result.
Good article, Sabine. You never know, maybe the funders have another think coming. Probably not, but maybe!
Jim,
ReplyDeleteWell, I've made my case already, many times. To recap it once again. Experiments have gotten very costly, we have to be very careful where to invest money, "just do it" is not a strategy.
"More precise measurements on the H-atom spectrum - which was thought to be entirely consistent with theory at the time - revealed small inconsistencies. These helped to point the theorists in the right direction, and the result was QED."
ReplyDeleteYes, good example. Of course, those experiments were cheaper. Still, the cost of a collider is a drop in the bucket. If all nations spent as much on basic research as some nations do, we could build two such colliders. Or more.
Another example: Tycho's main observation which led to Kepler's laws and thus more or less directly to Newtonian physics was that the position of Mars was off by 8 minutes of arc. Before Tycho, probably no-one had ever even measured the position that accurately.
"There are also medium-scale experiments that tend to fall off the table because giant projects eat up money. One important medium-scale project is the interface between the quantum realm and gravity, which is now accessible to experimental testing. Another place where discoveries could be waiting is in the foundations of quantum mechanics. These could have major technological impacts."
ReplyDeletePlaying devil's advocate, isn't "could have major technological impacts" standard marketing speak for trying to get money for basic research without making any concrete predictions? I have nothing against technological impacts, but basic research should be done for its own sake, not least because this argument can be used to avoid funding research which has no "impact".
And what are some examples of major technological impacts which could come from the interface between the quantum realm and gravity? Or from the foundations of quantum mechanics? Aren't these "predictions" just as vague as the ones you criticize. (Yes, quantum mechanics has had a huge impact, but just because it has had in the past doesn't mean that it will in the future. Just like with "beauty".)
As Pirsig said, the sad television scientist who says "Our experiment is a failure; we didn't find what we expected" is suffering mainly from a bad script-writer: if we know what we will find, why do the experiment in the first place?
Yes, money is not infinite, and even if more money for basic research is available in principle, it is often not in practice. Still, of all the ways one could improve basic research into fundamental physics, arguing against a new CERN collider would be pretty far down on my list.
Phillip,
ReplyDeleteYou make it sound as if potential impact should be a reason to not fund something.
Chris Bolger quoted Edmund Hillary as saying he climbed Mt. Everest "because it was there." Actually, it was one of first people who attempted to climb Mt. Everest back in the 1920s, George Mallory, who said it. He perished in the attempt, and nobody knows for sure if he ever made it.
ReplyDeleteBruce Knuteson solved the problem of quantifying merit of a scientifi experiment, see his paper from 2007 (I don't think that the community liked it then and I suspect that it won't like it now - I think he's right on the money):
ReplyDeletehttp://arxiv.org/abs/0712.3572
Gena Kukartsev
Sabine, I think you are "right on" in many of your criticisms, like: using misleading hype and specious arguments, and reliance by fundamental-physics theorists on the same kinds of arguments and approaches that have demonstrably failed in for several decades now. You back up your criticisms with your experience and observations in fundamental-physics research, and your arguments deserve serious consideration in thoughtful discussions.
ReplyDeleteHowever, in this posting and another recent one on the same topic, I think you are using your sound, technically-informed arguments as a "springboard" for arguments of a different character, moving into the political realm where you (I assume) have somewhat less experience and "insider" knowledge. You wrote to Jim,
Well, I've made my case already, many times. To recap it once again. Experiments have gotten very costly, we have to be very careful where to invest money, "just do it" is not a strategy.
What you are making in this statement is essentially a political argument rather than a technical one. At their root, funding decisions are political: governments, foundations and other sources of funding ultimately are driven by matters of national pride, prestige, curiosity, ideology, technological investment, productivity, societal demands, catering to "special interest" groups, and many other considerations that are best categorized as political. Desires of these kinds (and I'd argue that political issues are ultimately driven by individual and societal desires, not objective facts) cannot be objectively quantified -- by their nature they are subjective. Even the drive for greater productivity is subjective -- it relies on an assumption that high productivity is intrinsically good, not just good for certain groups. So a "cost versus benefits" argument against a new collider must try to quantify the benefits, but since benefits are ultimately measured by subjective criteria, such an argument is essentially political. Do you really want to to tread in the business of politics?
The other problem I don't think you acknowledge enough is that funding allocation is not generally a zero-sum game. Cancelling the SSC didn't suddenly free up billions for other physics research, as some people (like Philip Anderson) had hoped. It's only zero sum if a funding body or foundation allocates a fixed sum of money and leaves it up to the scientists to fight out the allocations. But (most, at least) governments choose funding amounts based on what programs they want to fund rather than allocating an arbitrary fixed sum.
I've read your article about the same topic in the New York Times, and that's why I am here.
ReplyDeleteAs I am not a physicist, I beg your pardon if I mess something up. But to me the LHC always seemed to be built partly in the hope that the Standard Model would break, and that experiments at the LHC would show the cracks. I remember one interview where one of the physicists wished for the Higgs Boson not be found, as this would be much more interesting than just finding the predicted particle.
Alas, the Higgs Boson appeared exactly where it was thought to be, and the Standard Model shines in all its glory and incompatibility to General Relativity.
It looks to me that now any "Beyond the Standard Model" physics has no place to hide anymore, at least no place humanity will be able to explore in the foreseeable future. The 126 GeV was the last reachable one to look for cracks, and now SM is solid for the next 15 or such orders of magnitude with no yet unknown but predicted particles a larger collider could hunt for. The "known unknowns" are exhausted, and any new collider would be built purely speculating on "unknown unknowns".
The new playing field for now seems to be the Weak Interaction. And because it is weak, you need billions of possible events to even measure one of it. This makes for a nice hiding place. But there is no guarantee that we will find something there, especially no guarantee for a weakly interacting dark matter particle. We only hope for it, because it would give us a way to detect it in addition to its gravitational effects on large scales.
Eric said :
ReplyDeleteThe only thing you could have written to cause more outrage than this would have been to write "Perhaps dark matter isn't a particle at all. Maybe it doesn't even exist." ;)
I'm not sure that this comment will pass, but Eric's passed, so maybe the door is open to the possibility that Dark Matter doesn't exist.
Particle theories have come up with a blank, even though the Lambda CDM Big Bang theories appear to favour a particle interpretation. Theories that continue to insist on the possibility of particle dark matter should probably stop trying higher energies and the ongoing theory is based on beauty and probably astray.
There are peer reviewed theories that do away with the need for Dark Matter or Dark Energy, but they do (mildly) violate Mass Equivalence. Anyone would think it a sin to think that scientific concepts such as equivalence could have boundary conditions.
Now. I am not blowing my own trumpet as the theories I am talking about are not mine, and I have nothing to gain personally by promoting them.
Yes. Maybe Dark matter doesn't exist. We should not be bullied into thinking that this statement is a scientific possibility.
regards
Marco Parigi
A "former professional Higgs Boson hunter" commented
ReplyDelete"BTW, I "predicted" years ago that M_H^2 ~ 1/2 m_t^2 which as far as I can tell was better than any SUSY based prediction..."
Are you the author of https://arxiv.org/abs/1401.3311 ?
I think, ultimately, there is no mountain humans won't climb, no cave they won't explore, no trick they won't try.
ReplyDeleteOf course they'll build a bigger machine. Bigger, better, faster, is what we do.
I think it's inevitable that we'll look at anything we can, any distance, any energy scale. It's not so much expectations, it's just seeing what's there, it's because we can.
Isn't even looking and finding nothing good science?
@sabine
ReplyDelete"Physicists have done nuclear fusion countless times in controlled environments".
This statement is factually wrong.
Fusion experiments (magnetic confinement) work with deuterium plasmas (DD) most of the time. That's enough to learn about the plasma physics involved at those high temperature. Only two machines have ever operated with deuterium-tritium plasmas (DT), which is necessary for fusion to occur, these being TFTR (now shut down) and JET. The reason is that tritium is rare, radioactive, and difficult to manipulate, not to mention that a DT shot entails quite substantial strain on today's tokamak, which needs to be "cleaned up" afterwards.
ITER is supposed to sustain rather long operating times with DT plasmas.
I'm too dumb to participate in the science of the debate in the comments... But surely the argument for a new LHC is just a cost-benefit analysis away?
ReplyDeleteCan it give any meaningful results that can be used by society... And if the value of this exceeds the cost. Build it.
Doesn't anybody else get the feeling we are going in circles here?
ReplyDeleteApart from the rather fruitless discussion, if particle physics may or may not make a big breakthrough soon, let's focus just for a second, what happens, if the new accelerator is not build and for the sake of it, the worst case scenario.
CERN would loose its reason to exist. Geneva would be happy, to get some very much needed space back. But Geneva would be unhappy to lose some very important organizations and input to the social life. France would be very unhappy too. But not for long.
The thought, that in 20 years, provided there would be some advancement in particle physics, everybody would flock back to CERN to start again, is like believing in fairy tales. Not gonna happen.
The other misconception is, that the money that would not go to CERN, would actually be available for other physics projects. Not gonna happen either. The pressure on governments to finance an international collaboration is much higher, than to finance national programs, which in most cases are only known to people, who are interested in that stuff and that money must be evenly spread to different programs (to quote TBBT, even geology). That money just would not be spent, because the national programs are already funded and the political pressure would be easily high enough to spend it on holes in the budget
Money spent on an international organization like CERN is much better spent, than on 150 national programs. Kinda "Economics of scale". If the new accelerator is dead, the possibility of finding something is also dead (provided China does not build one. If they build one and find something, we are all going to beg China for the results ... and in the end will pay a very high price for being cheap).
And all that is just a fraction of the price of loosing one of the most precious places on earth, where people from all kinds of nations, religions and what else, work peacefully together for a common goal to advance mankind. And do not forget the spin-offs, which have paid for CERN multiple times. We have much to loose and not a lot to gain from not building the FCC, but alone from the socio-economical point of view, it will again pay for itself over the long term.
Now please compare the prize of the FCC and HMS Queen Elizabeth and HMS Prince of Wales which everybody in GB thinks are absolutely necessary and their respective economical impact.
There are various people here who have tried multiple times to submit (in some cases identical) comments about their personal theories for something. Please save yourself the effort and save me the time: I will not approve such comments. Neither, for that matter, do I approve comments referring to personal websites. Thanks,
ReplyDeleteB.
Marty,
ReplyDeleteI realize that there are many non-scientific reasons that enter funding decisions. I am neither qualified to comment on those nor particularly interested in doing that. I simply want other people to have the information that I have.
Yeah, right, it's not a zero sum game. So if particle physicists ask for a big chunk of money but don't have good arguments and end up not getting it, then the rest of the foundations of physics may not benefit. We would therefore be well-advised to think about whether we want to leave the stage to particle physicists.
Opamanfred,
ReplyDeleteYes, you are right, they have not done it countless times.
Christian,
ReplyDeleteI have said this countless times, but here we go once again. If you are worried about knowledge transfer, you need a knowledge management plan. The LHC is not the only particle collider in the world, there are hundreds of this, so I consider it to be a straw man argument. If you are worried about CERN, please note that the LHC is not the only experiment they have, it's just the biggest and shiniest one (scroll down this page). So it's not like the place would be empty for 20 years.
If you are arguing that money should be given to large groups of people because they are large groups of people, that's a sure way to get "more of the same" science and have bad returns on investment. I totally know that this is what often happens (it is certainly not a problem only for particle physics) but it is detrimental to scientific progress.
If you want people to work together in peace on a common goal or such, you can do that on other projects. If spin-offs are what you are after, to begin with that's a poor motivation, but also there's no reason to think that particle colliders are somehow better at that than other science projects. (And please spare us the mentioning of Berners-Lee. I have debunked this argument so often just thinking of having to repeat it one more time makes me sick.) Best,
B.
I have observed how collaborating with CERN can be advantageous compared to collaborating with the US or China (for a small nation) because of the increased involvement of political actors and not just bureaucratic types. I am not sure if CERN would stay and have the same impact if no collider research was happening there. However, that will happen at some point irregardless of whether it happens in 20 years or 50 or 120.
ReplyDeleteFrom the recent discussions in several places, I see that beside the right time and the right place for "Lost In Math" the difference between the book events "Not Even Wrong", "The Trouble with Physics" and "Lost In Math" is the courage to say about "emperor's new clothes".
ReplyDeleteMitchell,
ReplyDeleteno I am not the author, mine predates that paper by 14 years. It was an aside in my standard Higgs colloquium/seminar from the period and not a formal theory based prediction. I remember a lively discussion it prompted at U-T Austin (yes, he was in the audience)
Fun times....
This may have already been mentioned/discussed; if so, apologies for the repetition.
ReplyDeleteWhat about China (Japan, India, ...)?
Any chance CERN could invite/induce them to join and pay for a big part of the cost of an FCC or similar?
If CERN/the EU passes (on an FCC, etc), and subsequently China (etc) goes ahead with one (for whatever reasons), how likely is it that CERN could join/contribute?
Are discussions like this/on similar topics happening in China? Japan? India?? If anyone knows of any such - whether in English, Mandarin, Japanese - could you give us a link or two?
"You make it sound as if potential impact should be a reason to not fund something."
ReplyDeleteNo, not at all, but the converse: just because something has no impact is not a reason not to fund it. The more scientists tout "impact" (or "potential impact") as a reason to fund something, especially fundamental physics which should be funded for different reasons and where there is no obvious impact, the easier it becomes to deny funding for things without impact.
Sabine wrote: And please spare us the mentioning of Berners-Lee. I have debunked this argument so often just thinking of having to repeat it one more time makes me sick.
ReplyDeleteBerners-Lee is trying to reinvent the web again. If he succeeds, CERN won't get the credit this time. :-)
Jean wrote: Are discussions like this/on similar topics happening in China? Japan? India??
ReplyDeleteI've been seeing reports that China is getting serious about building a collider that's about five to ten times more powerful than the LHC. It's expected to make plenty of Higgs as well as W and Z bosons.
Of course, there are always the optimists who say that the collider might produce "new particles never seen before."
Maybe it will inspire a new series of Crazy Rich Asian Physicist novels. The codename for the project could be Tunnel of Love.
@Steven
ReplyDeleteHistorically, ALL new colliders have produced particles "never seen before", so there's nothing to snigger about
There are still people making the 'actually this is cheap' argument above. In reality, it would take an appreciable amount of the overall European science spend, which is determined by politicians proportionally to the extent they see the overall enterprise of science as valuable to their constituents. If a new collider is funded then thousands of young scientists currently doing PhDs in biology, statistics, materials etc. will not get their excellent new ideas funded in future and may not be able to pursue a career in science. If nothing is found then we may get a political backlash against science generally and this will mean less research is done on cancer, renewable energy, sustainable materials etc. Fundamental research is very valuable but resources are finite - when a pure mathematician wants even a few thousand Euro they don't say "it's cheap and who knows what I might find?" they say some combination of (1) there is a realistic chance this will have some use in applied science (2) they will talk to the public and it is of public interest (3) the skills developed doing the research are needed by wider society. It looks an awful lot like collider physics cannot even make any such arguments.
ReplyDeleteDear Dr. Hossenfelder
ReplyDeleteThe LHC and who knows the FCC in the future are the "raison d'être" of the CERN. Without it, it is just another lab. Nobody needs the CERN without the big machines. The place would soon be empty without them (Running CERN on a lower budget just to keep it alive is really a waste of money). This does not have to be a bad thing. It would shake up the particle physics community quite a bit. The question is, do we want that? Is it worth the price of killing CERN? But building bigger hammers while not knowing where the nail is, seems not to be a sensible solution either. You seem to think, that I want to keep CERN as it is, which isn’t true. But I do not like the idea of creative destruction and therefore do not think, that not funding the FCC is the solution for the field of particle physics and the scientific community in general, because I like to look at the bigger picture and the impact it has on the whole, not just particle physics. But if CERN can not come up with a very good idea, why to build the next bigger hammer, well, close it.
My point is, that if the international community now financing the CERN stops funding the CERNs big projects, nobody is getting more money for other projects, because the money goes elsewhere.
I don't argue that money should go to large groups only, but it needs a large group to build a large collider. Small groups are not automatically more productive and as soon as you give a small group more money you get a larger group. Progress depends on the people involved and the organizational structure behind them, not the size of the group.
You are certainly familiar with the „Giesskannenprinzip“, which has been shown again and again to be a bad idea.
„If you are worried about knowledge transfer, you need a knowledge management plan“. I am not and you don’t need knowledge management to have knowledge transfer. But that is another topic.
Spin-offs happen more or less by chance. You can't be „after them“. We can only hope that they happen, but experience tells us, they will happen.
„And please spare us the mentioning of Berners-Lee. I have debunked this argument so often just thinking of having to repeat it one more time makes me sick.“
Humor me
Christian Tillmanns wrote:
ReplyDelete>And all that is just a fraction of the price of loosing one of the most precious places on earth, where people from all kinds of nations, religions and what else, work peacefully together for a common goal to advance mankind.
If I can elaborate on Sabine's response, after getting my Ph.D. in HEP theory, I went to work in industry. The first company I worked at had engineers born in China, India, Korea, Japan, and various other places.
We physicists, I fear, over-estimate how cosmopolitan pure physics is compared to other STEM subjects. Indeed, is it perhaps possible that we physicists often over-estimate our importance in the greater scheme of things in general?
Dave Miller in Sacramento
Unknown said
ReplyDelete"It was an aside in my standard Higgs colloquium/seminar from the period and not a formal theory based prediction"
Still, presumably there was some logic motivating the idea. What was that logic?
There is a profound sense in what Jean and Steven are saying, so we have to face the unease of open societies with Popper's optimism. However what Sabine Hossenfelder is saying certainly does not mean we have to reduce investments and funds for scientific research, but rather to spend them there where Science itself (with its instruments) offers a realistic prospect. In other words: if I have to find water in a desert using finite resources, I will not dig there where my instruments indicate that is very difficult to find anything else than sand.
ReplyDeleteWibble
ReplyDelete"Fundamental research is very valuable but resources are finite - when a pure mathematician wants even a few thousand Euro they don't say "it's cheap and who knows what I might find?" "
Very nice formulated.
Dave Miller in Sacramento
"Indeed, is it perhaps possible that we physicists often over-estimate our importance in the greater scheme of things in general?"
IMHO - yes.
Frankly to say, for instance molecular biology, genetics have far more value even for physicists, when they are in hospital.
Valeriy Tarasov
Sabine,
ReplyDeleteJust for objectivity, it will be interesting to see the public voting (probably in twitter) which field of science has priority for money funding.
Best
Valeriy Tarasov
https://www.scientificamerican.com/article/ghostly-galaxies-hint-at-dark-matter-breakthrough/
ReplyDeleteIt might be wise to spend money on big telescopes to find dark matter and dark energy. For 10 $billion, it may be best to put a huge telescope or a long baseline telescope array into orbit.
opamanfred wrote: Historically, ALL new colliders have produced particles "never seen before", so there's nothing to snigger about.
ReplyDeleteLet's not expurgate all of the failed and misleading predictions from the history. Haven't you been paying attention to the discussions in this blog?
By the say, I don't mind if the Chinese build a collider.
Particle physicists themselves fix higher and higher required energy levels, whereas their previsions fail, so that the new collider could have the same sort of the big infrastructure in Venice, MOSE, built to prevent lagoon tide but designed when G.W. effects on sea level were unknown.
ReplyDeleteI'm astonished at the number of people who want to frame the choice as "build a next-gen collider or stop looking for new physics". Equivalently, the number who pose it as "spend $20B because think what we might miss if we don't!".
ReplyDeleteDo people really not understand that funding is finite, and the actual choice here is between a next-gen collider and all the other things that $20B could buy and all the opportunities for discovery they would bring. So that's your choice, folks: a $20B collider that we have no reason to expect discoveries from, or $20B of other science that we do.
It's really not that complicated.
Mitchell,
ReplyDeleteit was related to the Higgs being composite and related to the top sector, nothing that deep. It was mainly a narrative foil for the SUSY phenomenology which was for all intents and purposes a religion at the time and I knew many of the high priests. SUSY did have some very interesting features but it was getting squeezed by the end of LEP II with Run II at the Tevatron dialing up the vise even further...
At the time, the existence of the "Chimney" up to the Planck scale in the Lambda vs MH suggested to me that we might be looking for the last fundamental particle to be discovered at a collider...
FWIW, SUSY probably does play role, but my guess would be that it is much closer to the Planck scale...
I guess Nature is not only subtle, but also malicious.
ReplyDeleteThanks for a very insightful article Sabine. Being bluntly honest isn't easy, particularly when there is so much money involved. Keep up the good work. :)
ReplyDeleteSabine, I think you are right to question 'yet another $20 Billion collider. But too gentle. In fact, as a model-builder, it looks to me like modern physics is in a crises of Kuhnian proportions, and has been for FAR too long.
ReplyDeleteMathematical equations of 'poorly understood attributes' (anything at all) may yet be useful for engineering purposes. But they do NOT stand up to the test of scientific validity required for causation and 'explanation' of real-world phenomena. You know, PHYSICS.
Not only that, but these equations apparently only apply in selected and narrowly defined scopes, and are apparently inconsistent with each other. What does it take, neon signs!? Surely such models are self-evidently bullshit!? Excuse me, 'of limited scientific value'.
You are far too accepting of the current snowflake experts whining about the entitlement funding due to their high reputation Status Quo positions in the public trough. Science, (and physics especially) is not an entitlement scheme for intellectual mediocrity.
Some might say that it doesn't matter that all the recent particles and the whole Standard Model are extremely unlikely to yield any sort of practical gadget - maybe the last particle that has been actually 'used' is the pion - for cancer therapy.
ReplyDeleteHowever, I suspect that it is practical applications that helps to keep physics grounded in reality. Even bad gadgets, such as the atom bomb, at least provide tangible evidence of something real.
This argument should have stopped HEP accelerator research years ago.
In the interim, while a new accelerator is on indefinite hold, perhaps some table-top experiments that might range from a few thousands to perhaps half a million dollars in cost would be worth pursuing. Specifically, I was thinking of some non-mainstream physics experiments conducted by both controversial and legitimate researchers. Back in the 90's into the first decade of this millennium, and even today, various individuals/research-groups made claims to detecting acceleration signals from superconductors subjected to certain conditions. The magnitude of these claimed signals ranged from several tens of milli-g's to about a kilo-g. The latter result was from a quite controversial and secretive figure, so credibility is definitely an issue in that case.
ReplyDeleteNonetheless, a common denominator underlay each experiment, despite differing experimental methodologies, and each group proffering a unique theory for their reported results. That common denominator was that a signal was only observed when the superconductor condensate underwent brief acceleration either mechanically or through the application of a strong electric field. Some time ago I did a simple back-of-the-envelope calculation relating claimed acceleration signal detected to the acceleration applied to the constituents of the condensate. Curiously there was a roughly linear relationship between applied/detected acceleration that spanned eight orders of magnitude.
My calculation, however, was based on a rather gross simplification, which may invalidate it. I assumed that both the nucleii and electron-pair condensate, within the bulk superconducting material, would experience a very small and sudden physical displacement; e.g. acceleration within the atomic lattice. I assumed the nucleii had a tiny wiggle range that immediately after the physical displacement would cause them to 'ring-down' back to their equilibrium positions. In fact, the data from Martin Tajmar's group (2003-2006), in hundreds of experimental runs, showed a 'ring-down' in the signal detected.
Anyway, maybe some research group would be willing to re-investigate this phenomena, while big-physics projects are on hold. I actually have my own ideas as to what could be the source of these signals (assuming they're real), which I won't divulge in respect of the rules.
I slipped up on the quoted low end signal magnitude stated in the 1st paragraph above. In most of the experimental runs, spanning the the years 2003-2006, the typical acceleration signal observed by the Tajmar group at the Austrian Research Center (ARC), was around 100 micro-g's, not ten's of milli-g's, as I recall. That would yield a 7 order of magnitude range from lowest to highest acceleration signals claimed to be observed. Unfortunately, the original paper is no longer on the arXiv, and a cursory check in my upstairs file cabinet didn't uncover the original paper, which I printed out years ago. I'll go down to the chilly basement later to check papers stored there. I know I have it, just have to dig around.
ReplyDelete