Two weeks ago I complained about the large number of dark matter experiments that hunt for hypothetical particles, particles invented just because you can hunt for them. Chad’s response to this is “Physicists Gotta Physics” and “I don't know what else Hossenfelder expects the physicists involved to do.”
To which I wish to answer: If you don’t know anything sensible to do with your research funds, why should we pay you? Less flippantly:
Dear Chad,But I admit it is unfair to pick on Chad in particular, because his reaction to my blogpost showcases a problem I encounter with experimentalists all the time. They seem to not understand just how badly motivated the theories are that they use to justify their work.
I find it remarkable how many researchers think they are entitled to tax-money. I am saddened to see you are one of them. Really, as a science communicator you should know better. “We have to do something, so let us do anything” does not convince me, and I doubt it will convince anyone else. Try harder.
By and large, experimentalists like to think that looking for those particles is business as usual, similar to how we looked for neutrinos half a century ago, or how we looked for the heavier quarks in the 1990s.
But this isn’t so. These new inventions are of considerably lower quality. We had theoretically sound reasons to think that neutrinos and heavy quarks exist, but there are no similarly sound reasons to think that these new dark matter particles should exist.
Philosophers would call the models strongly underdetermined. I would call them wishful thinking. They’re little more than guesses. Making these experiments, therefore, is playing roulette on an infinitely large table: You will lose with probability 1. It is almost certain to waste time and money. And the big tragedy is that with some thinking, we could invest resources much better.
Orzel complains that I am exaggerating how specific these searches are, but let us look at some of those.
Like this one about using the Aharonov-Bohm effect. It proposes to search for a hypothetical particle called the dark photon which may mix with the actual photon and may form a condensate which may have excitations that may form magnetic dipoles which you may then detect. Or, more likely, just doesn’t exist.
Or let us look at this other paper, which tests for space-time varying massive scalar fields that are non-universally coupled to standard model particles. Or, more likely, don’t exist.
Some want to look for medium mass weakly coupled particles that scatter off electrons. But we have no reason to think that dark matter particles are of that mass, couple with that strength, or couple to electrons to begin with.
Some want to look for something called the invisible axion, which is a very light particle that couples to photons. But we have no reason to think that dark matter couples to photons.
Some want to look for domain walls, or weird types of nuclear matter, or whole “hidden sectors”, and again we have no reason to think these exist.
Fact is, we presently have no reason to think that dark matter particles affect normal matter in any other way than by the gravitational force. Indeed, we don’t even have reason to think it is a particle.
Now, as I previously said I don’t mind if experimentalists want to play with their gadgets (at least not unless their toys cost billions, don’t get me started). What I disapprove of is if experimentalists use theoretical fantasies to motivate their research. Why? Think about it for a moment before reading on.
Done thinking? The problem is that it creates a feedback cycle.
It works like this: Theorists get funding because they write about hypothetical particles that experiments can look for. Experimentalists get funding to search for the hypothetical particles, which encourages more theorists to write papers about those particles, which makes the particles appear more interesting, which gives rise to more experiments. Rinse and repeat.
The result is lot of papers. It looks really productive, but there is no reason to think this cycle will converge on a theory that is an actually correct description of nature. More likely, it will converge on a theory that can be eternally amended so that one needs ever better experiments to find the particles. Which is basically what has been going on the past 40 years.
So, Orzel asks perplexed, does Hossenfelder actually expect scientists to think before they spend money? I actually do.
The foundations of physics have seen 40 years of stagnation. Why? It is clearly neither a lack of theories nor a lack of experiments, because we have seen plenty of both. Before asking for money to continue this madness, everyone in the field should think about what is going wrong and what to do about it.
This is quite a misrepresentation. Emphasis used to be placed on searches for specific particles predicted by specific, "beautiful" theories. Now, since that didn't work, the emphasis is on coming up with cheap experiments that can be used to look in a lot of directions at once.
ReplyDeleteThat is, instead of probing supersymmetry, you probe for, say, the presence of any particle of medium-ish mass which doesn't couple very weakly to photons. Or maybe the presence of a particle of low-ish mass which doesn't couple very weakly to gluons. The emphasis is on making as few assumptions as possible, to avoid getting "lost in math". And it goes without saying that every single one of these experiments has to be approved by funding agencies, with many ideas never getting funded at all.
This sounds like what you were arguing for as an alternative to colliders a few months ago, so why is it "madness" now?
Kevin Z,
DeleteI certainly never argued for this, and I do not know why you think so. I am sincerely quite shocked you could possibly have mistaken what I said for advocating something remotely like this. The major message I have tried to get across is: THINK! Unthinkingly spending money on "whatever" is the last thing I would advocate.
If you were serious about "making as few assumptions as possible" then you simply had a pressureless fluid and would, as I have said many times, focus on getting better astrophysical measurement until you know what dark matter is.
As I have said many times, here and in every one of my public lectures, what will happen if the current wrong ideals of beauty run into conflict with experiment but physicists do not reflect on what has gone wrong is that they will come up with another, equally stupid, criterion for producing theories. This is basically what we are seeing now.
Funding agencies rely on peer review, and peer reviewers will approve work that fits into their mindset, which is, to put it briefly "more of the same." This process results in a rich-get-richer trend. This has been much written about and is well-known, yet it still hasn't changed.
Well, I'm not sure what you say in your popular lectures, or in your very popular book, but your popularity doesn't change what's going on. Funding agencies act independently of physicists, and they're not happy to hand out money for no reason -- to say they spend without thinking is just insulting to them. Experimental proposals get rejected constantly, and even the good ones can take decades of prototyping and refinement to get the go-ahead.
DeleteOf course, astrophysical measurements are simultaneously being refined. That's the benefit of having more and cheaper experiments: you can do many things at once. For example, as I'm sure you know, anomalies in the center of the galactic halo can be explained if dark matter has a weak self interaction. That motivates indirect DM detection experiments. And those experiments themselves find excesses which could be DM, or which could be some other astrophysical objects in the background, which motivates a closer look at the background. Still others might try to explain these anomalies by changing the nature of DM, such as superfluid DM or fuzzy DM.
And this isn't even getting into experiments that don't just search for DM specifically, but can probe for any new particle in a certain mass and coupling range. For instance, black hole superradiance tests probe a wide range of very light masses, but cost literally nothing because they piggyback on what LIGO can already do.
From all of this, the last thing I see is a unified ideal. People are going in all kinds of different directions, motivated by existing anomalies, or upcoming experiments, or their own sense of aesthetics, or what new technology allows us to probe better. Of course, there is always the temptation to ignore these differences and treat physicists as one big unthinking monolith. As you know, that's the well-documented phenomenon of outgroup homogeneity bias; it is the _default way_ we view groups. Good popular science writing should counter this bias by showing nuance, not playing further into it.
Kevin,
DeleteYou erroneously claimed that I have argued in favor of "cheap" experiments that "look in a lot of directions at once".
I hope I have managed to clarify that
(a) I never said experiments have to be "cheap" (whatever exactly you mean by that. I have merely said that if an experiment is extraordinarily expensive it requires extraordinary reasons to justify the investment, and
(b) I never said we should "look in a lot of directions" I said think before you decide what direction to look.
As to the astrophysical arguments you mention. Yes, exactly. That is the kind of argument that must be made more watertight. (Not only the one you mention of course, but adding in other data.)
"Of course, there is always the temptation to ignore these differences and treat physicists as one big unthinking monolith. As you know, that's the well-documented phenomenon of outgroup homogeneity bias; it is the _default way_ we view groups. Good popular science writing should counter this bias by showing nuance, not playing further into it."
I have criticized very specific problems. You are the one who is now talking about something I have clearly not been talking about. In other words, you are ignoring the nuance in my writing and then complain about your own ignorance.
My humble solution: Fire theoreticians and hire more physicists doing direct experiments and observations; the real problem is in the armchair far detached from Reality theoreticians that appear to "lead" and create more obfuscation on top of the existing mess. Start by firing Sabine, too much talking and zero action.
Delete@Jeremy Jr. Thomas: In most areas of physics, there is a synergy between theoreticians and experimentalists ... the theoreticians propose some experiments, and interpret the results of the experiments; the experimentalists figure out how to do the experiments, propose some other experiments. This process is working very well in most areas of physics. But it has broken down in high-energy physics because the experimentalists haven't found anything, and the theoreticians don't have a solid experimental foundation to base their theories on. So is your proposal to hire more experimentalists to do more experiments that still won't find anything?
DeleteI don't actually have a solution to this. But I think firing the theorists and throwing more money into experiments isn't necessarily going to get us any farther. If the new experiments don't find anything, we won't be any better off than we are today. And if the new experiments do find something, then we won't have any experimentalists to interpret them.
DeleteI am a little worried that young theoreticians, who have not had solid new experimental data to base their theories on for over 30 years, might not know what to do with real experimental data. But we can cross that bridge when we come to it.
@Thomas: Experimentalists already outnumber theorists, in many fields overwhelmingly (10:1 or higher), which is just as it should be. I doubt that changing the ratio to 100:1 will help. Most funding in particle physics already goes to actually buying the nuts and bolts and superconductors that go into experiments, not to people in armchairs. Theorists do get a lot of press though.
Delete@Shor: There's definitely a divergence happening. I have lots of friends starting in formal theory that pride themselves on not knowing anything about real experimental data -- many people my age will say the real point of studying quantum gravity and whatnot is its mathematical appeal, not whether or not it's related to our particular universe. But you also have communities of phenomenologists that thrive on new experimental data and work side-by-side with experimentalists. Certainly the skill is not being lost. In any case, building a model is infinitely easier if experiments already are hinting at it.
@Sabine: The experimental landscape now is so different than 10 years ago. I don't believe that one can "just think" and pin down exactly the right way to go. I'm sure you thought carefully and found a promising direction, but I think I've done the same, and found a different one. A lot of older people have completely changed their research programmes, and I don't believe anybody could do that without serious thought. People have thought and scattered in all directions, which is the exact opposite of unthinking following, and just what a field in difficult times needs.
Kevin Z wrote:
Delete>And it goes without saying that every single one of these experiments has to be approved by funding agencies, with many ideas never getting funded at all.
Kevin, have you ever heard of a funding agency not spending all the money that has been appropriated, even if they have no productive way to spend it? I.e., have you ever heard of a funding agency saying, "Hey, we can only find a good use for a third of this money; please take the rest back!"?
I'm afraid that the fact the funding agency approves an experiment merely means that the unapproved ones were more unworthy. It does not prove that the approved experiments were worth the money but merely that the funding agency does not want its budget cut for next year, which is what would happen if they gave most of the appropriated money back.
By reading some posts here you may get the impression that experimentalists and people making observations do not have brains and they "need" a theoretician to "interpret" what they observe. The dark matter phenomena was discovered by observations and still theoreticians are unable to find a way to accommodate this new fact with their preconceptions; and this is just one example.
DeleteSo experiments and observations always will find new irreducible facts or phenomena that the existing theories will be unable to predict or even explain. Theories as theoreticians are always limited by assumptions and preconceptions respectively.
Real new discoveries are unpredictable and nothing can replace the constant observation and testing of Reality. Science starts and ends with empirical evidence in a never-ending process.
Kevin,
DeleteWell, I am glad to hear that. My blogpost was not a response to you. I hope that in making your decisions you have taken into account how your interests and judgements have been affected by having being part of a community of likeminded people probably for decades. Could you please let us know what measures you have taken to prevent biases from creeping into your assessment? What outside opinions have you drawn on? How have you avoided begin affected by the shared-information bias? Which steps have you taken to limit motivated reasoning?
And after you have told us that, why don't you tell us what experiment you think the community should do and why? What do you hope to achieve and what makes you think that's plausible?
Jeremy,
DeleteDark matter was discovered 80 years ago. The fact that we still don't know what it is, and that for 40 years experiments searching for signals of new (bsm) physics led to nothing, demonstrates that your idea that we don't need theorists and hey, let's just measure things simply does not work.
I did a lot of reading about what has worked and what has not, drawing on old papers, books on the history of physics, the philosophy of science, some statistics and epistemology, and of course all the contrarians I could find. I did this during two gap years, intentionally after getting a strong grasp of QFT and the SM, but before doing any BSM research of my own, so I had nothing to cause motivated reasoning. (Actually, I still don't; my PhD starts in the fall.)
DeleteIn the end I came to two conclusions: first, that naturalness is a good principle, even if it's stated wrongly most of the time, and second, that the real danger in physics is "what else could it be" reasoning. This is the phenomenon of latching on to the first reasonable explanation of something and dismissing equally simple alternatives as "contrived" or "unphysical", and if that first explanation turns out to be correct, acting as if it were the only reasonable possibility all along. Even the road to the SM, which is often portrayed as inevitable, is littered with hundreds of wrong and forgotten models which were perfectly reasonable at the time. And we had to have created those wrong models, or else we wouldn't have arrived at the SM at all.
What you see all the time is that, given two theories that both add, say, one new field and three terms to the Lagrangian, and achieve the same thing, one might be called elegant and simple, while the other might be called ugly contrived make-work for model builders. Everybody seems to make these kinds of judgments, both model builders and people who hate model building, but I don't think they have any real logic behind them. That's why I support looking in as many qualitatively new directions as cheaply as possible. There are too many equally simple things to test individually, including countless theories nobody has thought up yet.
That ocean of possibilities is why I don't think we can just think our way out of this situation, or even just think of a few experiments to focus on. If we somehow did, that would just be the same false confidence that got us into this mess, because the only true source of confidence is experiment itself. If we don't have just one place to look, we need more experiments, and stranger ones.
Kevin,
DeleteThis is awesome. Please tell me what makes you think that naturalness is a good principle because I have not been able to find a single case in which it worked. (I thought the charm quark was the one case for which it worked, but I recently dug up the papers again and came to the conclusion that actually it's not an argument from naturalness.)
Also, you seem to be saying that there simply is no good criterion for hypothesis pre-selection which ignores what I just told you above, namely that relying on consistency has consistently (ha) worked in the past. Again, if you see something wrong with that, please let us know why it is wrong, rather than just ignoring it and insisting on your opinion.
I feel that it is an illusion to think that fields like condensed matter are any better just because the experiments are easy to perform. The ifs and buts and simplifying assumptions are so many and the systems are so complex that agreement with theory and experiment may well be a fluke and we shall never know for sure.
DeleteI'm late to this string so apologize for my late comment.
DeleteRe: Kevin Z...."There's definitely a divergence happening. I have lots of friends starting in formal theory that pride themselves on not knowing anything about real experimental data -- many people my age will say the real point of studying quantum gravity and whatnot is its mathematical appeal, not whether or not it's related to our particular universe."
So why should I, as a tax payer, fund these physicist/mathematicians? If, seemingly, they do not seek to advance our knowledge of "our particular universe" it seems to me they are doing it for their own interest/amusement.
I understand that research in basic mathematics can lead to useful insights and advancements in our store of knowledge, but I agree with Sabine (if I understood her correctly) that before we fund something/someone we need to know just what they are planning on doing and where it might benefit humanity in general. If it is just something they are interested in I suggest they seek funding from Mr. Gates, or Mr. Bezos, or Mr. Walton et al and leave public funding available for some targeted goals. I'm not against basic research but do think that it should have a goal.
Physics was about understanding nature. The problem is that old physicists have been so successful that new physicists now do a new job: speculating about possible new physics.
ReplyDeleteAlessandro,
DeleteYes, there is that. Physicists have been so successful that further improvements are difficult. There is also, however, an unwillingness to even attempt the difficult.
As I said yesterday, but mangled the wording a bit, the theoretical game board is far larger than in the day of Wolfgang Pauli when he proposed the existence of a neutral light mass particle, circa 1930. The only plausible choices with the decay of a neutron was there exists some unknown particle or conservation of momentum is wrong. The first is the least extreme, and it turned out to be right. Today we have these open questions concerning the odd parameters of the standard model and dark matter, but not a lot of an anchor to hang on to. So the range of possibilities for new physics is immense.
DeleteRecently primordial black holes were ruled out as a significant candidate for dark matter. It appears that WIMPs may be ruled out as well. As Arthur C. Doyle's Sherlock Holmes put it one must examine what appears to be the most plausible cause, and if that is ruled out you go to the next plausible until eventually you deduce the cause. There does appear to be a pretty wide field for where DM might be. It could be a long search.
Sabine, and if the problem with the elusive dark matter is that its nature belongs to one of the WIMPZILLA sterile candidate hypothesis https://arxiv.org/abs/hep-ph/9810361? In such a case what would then be in your opinion the epistemological consequences of this particle in a practically unreachable energy range?
ReplyDeleteRegards,
Samuel.
And if science communicators with a PhD in astrophysics communicate about how dark matter could be the all abundant and available energy source of the future, stacking uncountable unproven assumptions, then things are getting worse in stead of better.
ReplyDeleteThe avarage layman reader believes just about everything that an astrophysicist says about his particular field, that comes with great responsability.
Personally I took an interest in physics, thinking this was a beacon of integrity, and a section of human endeavor marked by a noble search for progress. And certainly that is still part of it, but I had no idea that fashion and marketing were so deepyl engrained in the very fabric of it.
Pretty soon we'll have Dark Matter Cola, and Dark Matter will be the next sponsor of the World Cup Football ,).
https://twitter.com/StartsWithABang/status/1146298009338204162?s=19
I agree, what a load of bullshit. The stuff, if it exists, is extremely hard to even detect. How is one supposed to "harness" it?
DeleteI read the paper on this dark U(1) force or the dark photon. In some ways it is not that bad an idea. It would seem to me better if they has said there is U(3) = U(1)×SU(3) paired up with QCD. This additional U(1) might then be proposed, and is more parsimonious than the phenomenology of this paper.
ReplyDeleteThe problem with theories now and in the past is the playing field of theoretical possibilities is far larger than it was when neutrinos were proposed. This means the number of things likely to be falsified is much larger. In fact stuff that is wrong is clearly growing far more rapidly than stuff that will turn out to be real.
"This results in a lot of papers. It looks really productive, but there is no reason to think this cycle will converge on a theory that is an actually correct description of nature. More likely, it will converge on a theory that can be eternally amended so that one needs ever better experiments to find the particles."
ReplyDeleteThat sounds amazingly spot on. Sabine, I think you help to crystallize the thoughts of many scientists, who see high energy physics as an irrelevant subject that is incredibly hard to shut down.
My gut feeling is that science needs a greater link with technology in order to ground it. If we were routinely flying spacecraft around our galaxy, we would really need to understand whether gravity follows a MOND-type law, or if dark matter exists, and we would have a ton more data with a much higher quality to use to help that understanding.
Thank you for pointing out that feedback cycle. I think such a feedback is not a bad thing, since it is like asking a question and trying to answer it - but maybe there is an intermediate state that is missing, namely a pre-selection for questions that are not well motivated. In this sense, how would you rate the peer-reviewing process for theoretical papers? I feel like if this is done properly, many things can be ruled out quite in the beginning.
ReplyDelete“Philosophers would call the models strongly underdetermined.”
ReplyDeleteNotice Sabine that you were forced to merely say “would” here. Apparently philosophers don’t yet endorse your position. This might be because they don’t give a shit (and even philosophers of physics?). Or it might it might be defensive given how easy it is to criticize philosophy. (People who live in in glass houses…) Regardless apparently you can’t depend upon philosophers to fix physics — “Munich” endures!
You may shame physicists like Chad Orzel for saying “Physicists gotta physics”, but is it really their faults? Epistemology does not reside under the domain of physics or any science. It resides under the domain of philosophy. Thus in order to fix physics, and indeed all of science, we should need a community of respected professionals with generally accepted principles of epistemology (at minimum) from which to guide the function of science.
If philosophers cannot figure this sort of thing out, then fuck ‘em — we must start our own community. And what would be decreed? I’d suggest my second principle of epistemology to begin:
“There is only one process by which anything conscious, consciously figures anything out. It takes what it thinks it knows (evidence), and uses this to assess what it’s not so sure about (a model). As a given model continues to stay consistent with evidence, it tends to become progressively more believed.”
Your second principle fails to address the question of how to test if a given model 'stay(s) consistent with evidence' when the evidence itself is lacking. Do we wait for 'evidence' to arise out of the normal course of events or specifically construct tests against which the model can be tested?
DeleteIs the existence of a model sufficient of itself to justify attempting to generate further evidence against which the model can be tested? The answer most would agree I think is no. But that of course generates a whole debate about the criteria used to validate research funding and resource allocation.
“Your second principle fails to address the question of how to test if a given model 'stay(s) consistent with evidence' when the evidence itself is lacking.”
DeleteThanks for your interest RGT. Well my EP2 does at least implicitly address that issue. It concludes, “As a given model continues to stay consistent with evidence, it tends to become progressively more believed.” Thus the less corroborating evidence that a given model has going for it, the less believed it should tend to be. So science concerns both developing models, as well as testing them. Though it may be fun to fantasize about a given model, that’s simply not sufficient.
One thing to keep in mind regarding the debate about the criteria used to validate research funding and resource allocation, is that the human is naturally self interested. It tends to rationalize justification for whatever it perceives to be in its own best interest. My perception is that lots of people in the physics community have been hoping that Sabine was finally being kicked out of their club. Presumably they could then stop worrying about her inconvenient observations. So now with her three year extension apparently Chad Orzel has written this pathetic article to rally the troops.
In the end however I suspect that her efforts alone won’t be enough. I believe that we’ll need to develop a community of respected professionals with generally accepted principles of metaphysics, epistemology, and value, from which to better found the entire institution of science.
If a respected group of scientists does come together to form such a community, then this should naturally enrage philosophers. How dare scientist try to show them up! As I’ve already said, the human is naturally self interested. And once again, fuck ‘em! They can either get on board, or prepare for a coming war. Science is a young institution. Its mechanics are going to get straightened out regardless of various conflicting political interest.
It's time to rethink. Modern physics is a bunch of believes, they call them hypothesis, and then they stack hypothesis over hypothesis until they have forgotten that the base wasn't sure.
ReplyDeleteStart with the physics before the begin of the 20. century, a time from which a lot of unfortune and nonsense came over us.
There is money enough. But the community fears to lose its credibility. But that's no sincere motivation for scientist.
It’s a big industry. There are a lot of people encouraged to study for a career in physics, a lot of students working hard toward a career in high energy particle physics. The work environment they find when they arrive is what it is. If theoretical particle physics is in an hiatus, they have to do something. If you wilfully sabotage your own job, your wife will kill you, your children may be disadvantaged.
ReplyDeletePerhaps more is needed than pointing out deficiencies. Champion myriad alternatives.
Think of lots of tiny projects. Put detectors on top of mountains. Then again instant coffee in a chilly kitchen in the Atacama may be less collegial than the CERN canteen.
Voluntary or involuntary redeployment of postdocs happens annually. Might science funding bodies have enough power to redirect surplus particle physicists (and string theorists) toward the ignominy of condensed matter physics, or worse , to retrain as engineers?
With few alternatives offered, large parts of the particle physics industry are not going to volunteer to self-destruct. Criticism directed at the industry will be politely contained. To make a difference criticism should be directed outward, to where budgets are set and controlled.
And to effect change requires a willingness to be truly, deeply disliked. Sabine is too nice. She will be contained.
Hello Sabine,
ReplyDeleteChad asked you a number of excellent
specific questions in his piece,
could you please answer them?
What exactly entitles you to a further
three years of being funded?
For Chad and myself it is a heavy teaching
load...
Franzi,
DeleteYou get research grants because you teach? I don't understand how that works, could you please explain?
I rest under the impression that I have answered Chad's questions. If you think there is a question I did not answer, please let me know which.
I get payed for teaching, the research is extra!
DeleteWhat useful to the community are you doing
for your pay?
Here are some of Chad's question that you did not answer:
> Should fundamental particle theorists be retreating into monastic seclusion, vowing to produce no new work in existing
> paradigms until they come up with something better?
> I'm even less clear, though, on what experimental physicists are supposed to do while the theorists radically restructure
> their field. What does it mean to "think more carefully before commissioning experiments to search for hypothetical
> particles"? Just sit around and wait for the theorists to emerge from seclusion, like one of the outer layers of the concents > in Anathem?
Franzi,
DeleteI do the research that is stated in my contract. I work at a no-teaching institution and do not have teaching duties. What useful to the community am I doing? I carry the average burden of peer review, organization, administration, and mentoring.
I also, in case you missed it, spend some time on science communication. If you want a pissing contest, there are almost certainly more people who have learned science from me than have learned science from you. And I do that unpaid, thanks for asking.
As to the quote from Chad. I answered this question, but evidently I was not clear enough, so please allow me to repeat it: Think. I cannot do the thinking of some thousand of people. If these people do not know what to do, or cannot come up with reasons why their research is worthwhile, then we should stop paying them.
Look, we both know that Chad's referral to "monastic seclusion" is a deliberate exaggeration with the attempt to ridicule me. What people should do is have a hard look at the reasons why they decide to make this particular experiment or work on that particular theory. How much have their decisions been influenced by the stories that get passed around in the communities they are part of? How much of their decisions can they really rationally justify? How much of it is based on non-scientific criteria that, if you look at recent history, worked badly and should be retired?
That's some suggestions for thoughts you may want to start from.
Hi Sabine
ReplyDeleteThanks for this thread. I was just about to make a post on my favorite site which is physicsforums about experiments. after many years and of course being armchair so called I was appalled that there actually so few experiments ABOUT fundamental physics. Lately we were discussing an interpretation called "thermal interpretation" which claimed that the energy we measure is not an eigenvalue but an expectation value of the energy spectrum. I was surprised that this was very hard experiment to do to achieve distinction between the two.
Overall there seem to be very few if any experiment that actually shed some light on fundamental physics. Young experiment itself is so controversial since it is not known how the spot actually is created on the detector.
take this experiment for example which the title seem so far away for the conclusion.
https://www.nature.com/articles/s41586-019-1287-z
Moreover, There is only one experiment that claims that it had recreates the hydrogen wavefunction!! and I have read about many experiments that are considered to be very hard to do this for even the simplest situation, I will dig them up when I have the time (that shows how rare these are and not clear at all if indeed are about fundamental physics i.e. interpretation/understanding)
ReplyDeleteHi Sabine, I think the first time I read about "40 years of stagnation" was in 2012 or 2013 - just after the Higgs detection. Should it be 46 now? (1973-2019)
ReplyDeleteBest,
J.
It's impossible to put an exact number to this because
Delete(a) the standard model wasn't completed any particular day and it's somewhat debatable just how old it is. Weinberg recent wrote an anniversary essay that actually puts it at half a century of age, and I suppose if anyone knows then he knows.
(b) Maybe more importantly, there's the question at which moment ignoring that a method does not work becomes pathological. See, when physicists in the early 80s started thinking about grand unification and supersymmetry and string theory and so on, that made total sense at the time. But then this didn't work, several GUTs were ruled out and amended, axions were ruled out and amended, dark matter searches returned consistently nothing, supersymmetry and string theory had to be patched over and over again to avoid confict with observation -- and at exactly what point do you say enough is enough?
So I vaguely say 40 years. But if someone wants to make a case it should be 35 or 45, I wouldn't disagree.
Sabine, How do you suggest the money be spent?
ReplyDeleteIn New Jersey (where I live) we would say that "they got nothing".
ReplyDeleteIt seems to me that also the foundations in question are some kind of make-up.
ReplyDeleteIt is interesting a lot of this comes down to money. It comes from this age we are in where socialism is a REALLY bad word. God forbid, particularly in USA, that we should have anything to do with socialism.
ReplyDeleteNever mind that while universities are socialist institutions for intellectuals the military is a socialist institution for soldiers. Academic science departments are in a way socialism for scientists, but they are also welfare-socialism for corporations eager to externalize costs. Public schools are socialism for teachers and police departments are socialism for those who like to use force. Road construction is socialism for contractors and building laborers, while wildlife preserves are socialism for park rangers and eco-biologists.
So take your choice; it comes down not to socialism or not socialism, but which form do you like or dislike. Maybe some dislike the idea of spending money on dark matter searches, but want that new arts-performance space. Then there is the mother of all socialism, the military and at times it gets to spend a lot of money killing people and destroying things.
I do not disagree. In the US of A here many people have gone a bit manic over this. There has been this patchwork of rather unrealistic to insane ideas generally called libertarianism that cites most or any use of public money obtained through taxation as a form of robbery.
DeleteMost people who work of programs funded in a public manner see their efforts as positive. In a representative system it is presumably up to people to make choices for what they think is valuable.
In the US of A things have gone a bit off the rails, where a lot of people object to any sort of funding of this sort, except maybe military and police. When it comes to big questions, either abstract in a scientific manner or practical such as global warming, many think it does not matter for Jesus is coming back and He will set things right. When people are thinking stuff like that you have to figure something has gone horribly wrong.
Sabine,
ReplyDeleteI felt like, after reading Chad's article (even on Forbes, always a painful experience!) that he had a valid and clear rebuttal. And after reading your response, it did not seem to quite address Chad's central arguments: (1) that experiments are not really designed from theories in the first place. And (2) that useful criticism here is of a sort that promotes overlooked experiments in place of over-funded ones.
These proposed experiments are *not*, usually, motivated by theories but are born of ideas for how we can test the universe in some new way using some new technology. Experimentalists are usually unconcerned with or unaware of most of the theoretical work going on (to a fault). The theories cited are usually found *after* ideation, and are just thrown in to improve chances for funding. Or, less pessimistically, to better engage in the larger scientific dialogue.
A productive experimental physicist ought to be doing just this: Think of a new kind of experiment in a process akin to brainstorming. Then look to the larger community, including theorists and then funding agencies, for critical evaluation and selection.
The job of the funding agencies, in principle, is to both advocate for science and also to best use the funding they have by picking those experiments that collectively represent both diversity and promise. Of course the valuation of "promise" is simply impossible to do correctly without hindsight. But of course a promising experiment is one that can reject as many untested theories as possible either with or without regard to the quality of those theories. That, or experiments that might promote technology in some way that might enable even more promising experiments in the future.
So I think I'd feel more enriched to read opinion pieces here that take on more of the role of advocate: "Here is a proposed experiment, overlooked by our broken and myopic scientific systems, that's cheaper and/or more promising than this or that."
I'm sure you'd agree that funding for basic science has been on a steady downward trend, globally, over the past 30 years. And that the current level of funding is not in line with the importance and promise of the field. So it's not that we should stop experimenting altogether, but that we should be using our scarce research moneys in better and more promising ways. What are those better ways?
I think your arguments against the feedback loop of publications-leading-to-more-publications sometimes ignores the perspective that papers are just a form of public conversation between scientists. They might be motivated by funding, which is a problem, but they should mostly serve to document and share what scientists are doing and thinking. It's perfectly natural for this conversation to go back-and-forth, be messy and often wrong.
Topher,
DeleteAaand once again someone comes to complain that I do not deliver a list of experiments that should be done. And of course if I did come up with such a list you would criticize me for doing exactly this, wouldn't you?
Let me say this once again: I am one person. It is literally not my job to evaluate potential project proposals of a 10,000 people community. And even if I could do it, I shouldn't do it. Your insistence that I should is insincere. You make it only to have something to complain.
I have no problem whatsoever with conversation going back and forth, sometimes being messy or wrong. I do not know what makes you think so. The problem is that unless scientists take into account that conversation begets more conversation regardless of the scientific value of that conversation's topic, they will continue to blow bubbles of useless research.
As to your other complaint that I didn't comment on Chad's claim that experiments aren't designed from theories in the first place, I did address that point, of course, you just chose to ignore it. I said that it's all fine with me if experimentalists explore whatever they think is worth it. I am saying they should not motivate their search with invented particles because that creates a feedback loop. Maybe read it again since you seem to have missed it.
Sabine your arguing style is polemic. When challenged, even by well laid out arguments, you resort to demanding a burden of proof from them. I refuse to judge this debate as my knowledge is to poor but I have managed to understand their counterpoints due to their structure while struggling to understand what you are proposing.
ReplyDeleteYou are advocating change so if anything the burden of exposition is on you.
It will be interesting to see how you respond.
Michael,
DeleteCan you please be clear what it is that you do not understand? I can't explain something if I don't have a question. Have you factored in that the reason you understand what you call "counterpoints" (which?) is that you have heard these multiple times?
As to polemic. I am not talking about my writing style, which you may or may not like. I am saying that this isn't an argument I am making to insult someone and I am frustrated that people take it as such rather than thinking about what I am saying.
I've read many of Sabine's essays, and I think it's fair to say that her criticisms come across as more of a personal gripe than an objective assessment of the direction physics is heading. The notion that physics should focus on testable predictions and experimental verification is exceptionally myopic and misses the entire point of what physics is about. Fundamentally, physics is about understanding the mathematical framework of physical law. After all, the greatest miracle in science is that the universe can be explained mathematically. As a theoretician, I'm less interested in finding (or not finding) a new MSSM particle, for instance, than exploring the connections between seemingly disparate and conflicting areas of physics such as GR and QM - and the test bed for those ideas is purely mathematical. In fact, some of the most abstract mathematical concepts like group symmetries, topology, and algebraic geometry have been the driving force behind physics for decades. The reason for this is fairly straightforward: All of the physics that lies between the GUT scale and the Planck scale will likely never be directly accessible to experiment. Even so, the past twenty years have been enormously fruitful in advancing our understanding of the laws of nature. I would even go so far as to say that this is perhaps the most exciting and productive time to be a physicist since the early half of the 20th century.
ReplyDeleteIn short, there is no "crisis" in physics. All this whinging about getting lost in math does is play into the hands of the science-denier crowd and paint a very misleading picture of the goals of science.
CWebster,
DeleteWell, thanks for illustrating the problem. You get top scores for
(a) launching with an ad hominem attack
(b) confusing math with science
(c) accusing me of being "exceptionally myopic" while at the same time declaring that "all of the physics that lies between the GUT scale and the Planck scale will likely never be directly accessible to experiment", which is an incredibly ill-informed comment, and
(d) simply denying the utter lack of progress in your field
Congratulations!
Sabine, the real problem seems to be that you refuse to acknowledge or accept any opinion contrary to your own, which is hardly in the spirit of scientific discourse. And conflating science with mathematics? Seriously?
DeleteAt the end of the day, the relationship between physics and mathematics is so deeply intertwined that what we generally think of as the physical world may have no more objective reality than the square root of negative one. And as physicists, that's not really up to us to decide. We can construct all sorts of toy models that have no bearing on the "real" world (as far as we understand it) and yet still gain important insights into our own universe, because physics in the 21st century is as much about the process as it is about making testable predictions. Physics is not stagnating in the La-la Land of mathematics, it's merely evolving.
Take the string landscape, for example. The fact that the myriad solutions of string theory don't uniquely describe our own universe is often touted as "evidence" that it's nothing more than a mathematical boondoggle. On the contrary, given that string theory is the only mathematically consistent framework that encompasses the Standard Model which not only predicts, but requires, gravitation, that tells me that we're almost certainly on the right track and that string theory as it stands now is either simply underdetermined from our ignorance as to what additional constraints to apply to it, or that all the anthropic arguments, whether we like them or not, are indeed true, and our universe is only unique to the extent that we're here to ask such questions to begin with.
As for a lack of progress, that's simply an outright falsehood rooted in your own prejudices. What exactly is your metric for progress, anyway? The way science works, since you don't seem to understand it, is that if you disagree with the direction things are moving in, you put forth your own alternative ideas and allow them to be judged on their merits by your peers. I see no evidence of that whatsoever. As a matter of fact, I see no discernable difference between your work and the highly mathematical approach you take umbrage with. And that's sort of the point: All of these mathematical machinations are no less useful or important than good old-fashioned pragmatic experimentalism. There are many things I happen to think are blind alleys in the theoretical literature, but unlike you I would never suggest to my colleagues that they quit pursuing them, because they could very well lead to other more interesting discoveries.
Now, I'm sure you're going to fire back with yet another vacuous, knee-jerk "nuh uh," but in order to sway those of us who are highly skeptical of your criticisms, we'll need to see something slightly more substantive - because I, among many others, are just as firmly convinced that we've made more progress in the field of quantum gravity in the last five years alone than the previous fifty.
Actually, I shouldn't even use the term "quantum gravity." All of the work on gauge-gravity duality over the past twenty years - AdS/CFT, the double copy, ER = EPR, Ryu-Takyanagi and the like - suggest that QFT and GR are merely mathematically equivalent descriptions arising from some more fundamental theory. (Hence my "incredibly ill-informed" comment about physics at 10^16 to 10^19 GeV, which, short of building a collider the size of the Milky Way, will never be directly verifiable. Indirectly, perhaps, from cosmological evidence, although I'm sure even that wouldn't budge Sabine.)
DeleteCWebster,
DeleteI totally 'accept' that you have opinions. Luckily science isn't about opinions.
"What exactly is your metric for progress, anyway?"
No change to the foundations of physics since the 1970s. Problems that were unsolved then are still unsolved. Methods of theory development that have failed repeatedly are still in use. I am making this short because I have said this literally hundreds of times in my blogposts and in my public lectures.
"The way science works, since you don't seem to understand it, is that if you disagree with the direction things are moving in, you put forth your own alternative ideas and allow them to be judged on their merits by your peers. I see no evidence of that whatsoever."
Ah, there's that again. If I would put forward an alternative, then of course you would criticize me for pushing an agenda. Besides, I do of course have my own research that I work on which isn't hard to find out.
"As a matter of fact, I see no discernable difference between your work and the highly mathematical approach you take umbrage with."
Quite possibly that's because you didn't understand what I am saying to begin with.
"There are many things I happen to think are blind alleys in the theoretical literature, but unlike you I would never suggest to my colleagues that they quit pursuing them, because they could very well lead to other more interesting discoveries."
Or more likely, not. How about learning from past mistakes? Does not sound good to you?
"in order to sway those of us who are highly skeptical of your criticisms, we'll need to see something slightly more substantive"
I've written a whole book about this.
"I, among many others, are just as firmly convinced that we've made more progress in the field of quantum gravity in the last five years alone than the previous fifty"
I have no doubt that you think this is the case.
CWebster,
DeleteYes, as I said, your comment about testing the Planck scale is incredibly ill-informed. You'd think that someone who seems to be working on quantum gravity should know that the Planck scale is dimensionful.
Readers of my blog know, of course, that I get this very comment, wrong as it is, frequently and have answered to it hundreds of times. Please read this for starters and if this doesn't clarify the situation, let me know.
And there we go with the dismissiveness again, because evidently we're all too stupid to understand what she's saying. Writing a 300-page book doesn't make your arguments any more plausible, so I'm not sure how that has any bearing on the discussion. I've read several of your papers, and while there are some good ideas there, you haven't exactly advanced progress in the field yourself, which is where I sense some of the frustration lies. Right now I'm looking at your 2017 paper on dark matter, and I can tell you that any sort of Verlindean modification of GR is a wild goose chase. Spacetime is not quantized, which I suspect is why there are only a few dozen people earnestly working on LQG. The whole idea that spacetime itself is discretized rests on an outmoded, overly idealistic reductionist paradigm that has no place in 21st-century theoretical physics. I suggest you contact Nima Arkani-Hamed and have a long discussion with him about all the fruitless attempts at modifying gravity, and how they inevitably run afoul of established physical law.
DeleteYes, the gravitational coupling constant is dimensionful. Length squared. What of it? You conveniently neglected to post my comment on that, then substituted your own interpretation, which is incredibly disingenuous.
Well I read your "When Gravity Breaks Down" link and you call me ill-informed. As I stated in another comment that you didn't post, QM and GR are not two distinct things; they're complementary descriptions of the same underlying physics. As far as attempting to put macroscopic objects in a quantum superposition, good luck with that. Gravitational entanglement doesn't work the way you think it does, and in fact that's the subject of a paper I have in pre-preprint. It's relatively straightforward to show that quantum gravitational effects vanish above the electroweak scale, which is why I said what I said. All the wishful thinking in the world won't make it otherwise.
DeleteCWebster,
DeleteLet me just note that your whole comment is an ad hominem attack that bears no relevance to my argument whatsoever.
I don't know what comment you are talking about that I supposedly didn't post. For all I can see, I approved all comments I received under the name CWebster.
(Oh, and I spoke with Nima about modified gravity, thanks.)
CWebster,
Delete"Gravitational entanglement doesn't work the way you think it does, and in fact that's the subject of a paper I have in pre-preprint. It's relatively straightforward to show that quantum gravitational effects vanish above the electroweak scale, which is why I said what I said."
Thanks for voluntarily disqualifying yourself from any further discussion.
It has to do with Yang-Mills theory and its relationship to diffeomorphism invariance. Mathematically, GR has an underlying local YM gauge symmetry. Maybe wait until the paper comes out before disqualifying yourself as a scientist by criticizing something you've never read.
DeleteAnd no, you didn't approve the comment I mentioned until after I called you on it.
Had you spoken with Nima, you wouldn't be pursuing modified gravity to begin with. You can get nice flat galactic rotation curves by asserting that Newton's constant is a function of the local matter density, for instance, but 1) there's no evidence to suggest that's the case, 2) it breaks everything else cosmologically, and 3) it reeks of artifice. Whatever pet theory you have for dark matter, the Occam's razor explanation is that it's an as-yet undetected MSM particle.
Btw, literally every one of your replies thus far has been ad hominem, so pot meet kettle. Given that your entire "argument" as you euphemistically call it is an attack on your colleagues' methodology, I'm not exactly sure what reaction you expected. "Oh, duh! Sabine is absolutely right. What were we thinking??" is not it.
Delete"Fundamentally, physics is about understanding the mathematical framework of physical law. "
DeleteThis phrase is a clear reflection of how far detached from Reality are some theoreticians.
If physics is about understanding the mathematical framework of "physical law(s)" who them will "discover" in the first place these physical laws? Are all irreducible physical laws known? Can we assume that we ever know all irreducible physical laws?
It seems that many theoreticians are afflicted with the "hammer's syndrome": for a hammer everything looks like a nail; and as a hammer has its limitations even Mathematics has its intrinsic limitations.
Sabine is very right: Nothing can replace the constant observation and testing of Reality; the irreducible physical laws that are the foundation of any theory or framework that pretend to describe Reality can only be found by a never-ending process of observations and testing of Reality; this empirical evidence has precedence over any existing preconceptions/theories and that is the only way to keep an objective approach to Reality and avoid the creation of String Theory cult-like approaches.
CWebster,
Delete(a) "And no, you didn't approve the comment I mentioned until after I called you on it."
Has it occurred to you that you maybe just missed it? I don't even know what reason I could possibly have to not post your comment.
(b) "literally every one of your replies thus far has been ad hominem"
False. You seem to not know what an ad hominem attack is. You have attacked me rather than the argument I make. That's an ad homimen attack. It's a logical mistake. I have, for all I can tell, not attacked you, both because I don't know who you are and because you haven't made any argument to begin with.
(c) "Had you spoken with Nima, you wouldn't be pursuing modified gravity to begin with."
Ok, let me see, you are claiming that I am lying about having spoken with Nima because I am working on modified gravity?
I think that's enough nonsense. If you want to continue this discussion, please sign with a name.
CWebster, by writing this: "The notion that physics should focus on testable predictions and experimental verification is exceptionally myopic and misses the entire point of what physics is about." have you just declared that physics is no longer a branch of science?
DeleteTo turn up the contrast, you are advocating that the SKA (to pick one example) be scrapped, because theoreticians like you will - one day - work out the details of what happened after the "dark ages", so there's no need to waste money actually looking? I'm pretty sure that's not what you are advocating; so, please let us know what role you think testable predictions and experimental verification do/should play, in physics.
"The notion that physics should focus on testable predictions and experimental verification is exceptionally myopic and misses the entire point of what physics is about."
DeleteThis has got to be the most hep-th statement I've ever heard. Such a statement would be rightfully dismissed without a second thought anywhere except for this small, isolated, and extremely unusual subsubfield of physics.
Jean,
DeleteI'm not at all suggesting physics should be a purely philosophical discipline or that experimental verification shouldn't be the ultimate goal of any theory. What I'm suggesting is that testability isn't necessarily a useful criterion in determining whether a particular theoretical path is valid, or indeed whether it's fundamentally correct. I also reject the notion that progress in physics is only made through experimentation. I would even argue that physics has matured to the point that empiricism alone is incapable of answering some of the most basic questions about the universe, and we're forced to rely on theory to provide those insights.
String theory in particular may or may not ever lead to a falsifiable prediction, but I'm certain of two things: 1) Physicists know more about the structure of the standard model, the origins of the four fundamental forces, and the relationship between quantum mechanics and gravity from string theory than from all of the other subdisciplines of physics for the past 50 years combined; and 2) mathematical physics has and will continue to spawn new ideas in other areas that *are* testable, like it has in condensed matter physics with topological QFT, for example.
And no, we theoreticians are not a small, isolated, or in any way unusual subfield of physics - we're quite mainstream and very much among the majority in terms of direction and methodology.
My reading of this is Sabine is urging us to think and consider all her arguments instead of having instant reactions to a summary blog. She has thought about this for a long time and laid out a case in books, blogs, talks etc. ‘think’ I.e research her entire body of work. Then reasonably you can state your case. Now there could be legitimate counter-arguments, but so far I haven’t seen one that specifically references her entire body of work on this concept and finds that she hasn’t addressed some of the question being raised. A blog post is an excerpt of work. So ‘think’
ReplyDeleteAll we theoreticians get paid to do is research and think - and Sabine certainly doesn't have the market cornered when it comes to rational thought, nor does she have any greater insight into the workings of science than the rest of us do. She's simply more vocal about her displeasure, which is fine. Alternative viewpoints are always welcome in science. But to borrow a quote from Amadeus, "You are passionate, Sabine, but you do not persuade."
DeleteCWebster,
DeleteI have laid out my arguments very clearly, whereas you have no argument other than that you don't like what I say. How about you give that "rational thought" that you talk about a try?
My argument is the work I produce, which advances the field in spite of your objections. That's how science works. You might consider that if others agreed with you and for one instant thought that what they were pursuing was pointless mathematical masturbation, they'd be smart enough to know when to quit and maybe take a different tack - because one thing is certain: Most of the people you're criticizing are at least as intelligent as you, so why should their reasoning be any less lucid than yours? We've listened to what you've said and we don't agree. And that, as they say, is that.
ReplyDelete