Sabineblogging
I’ve of course been following the recent public debate about whether to build a circular collider to succeed the LHC—notably including Sabine Hossenfelder’s New York Times column arguing that we shouldn’t. (See also the responses by Jeremy Bernstein and Lisa Randall, and the discussion on Peter Woit’s blog, and Daniel Harlow’s Facebook thread, and this Vox piece by Kelsey Piper.) Let me blog about this as a way of cracking my knuckles or tuning my violin, just getting back into blog-shape after a long hiatus for travel and family and the beginning of the semester.
Regardless of whether this opinion is widely shared among my colleagues, I like Sabine. I’ve often found her blogging funny and insightful, and I wish more non-Lubos physicists would articulate their thoughts for the public the way she does, rather than just standing on the sidelines and criticizing the ones who do. I find it unfortunate that some of the replies to Sabine’s arguments dwelled on her competence and “standing” in physics (even if we set aside—as we should—Lubos’s misogynistic rants, whose predictability could be used to calibrate atomic clocks). It’s like this: if high-energy physics had reached a pathological state of building bigger and bigger colliders for no good reason, then we’d expect that it would take a semi-outsider to say so in public, so then it wouldn’t be a further surprise to find precisely such a person doing it.
Not for the first time, though, I find myself coming down on the opposite side as Sabine. Basically, if civilization could get its act together and find the money, I think it would be pretty awesome to build a new collider to push forward the energy frontier in our understanding of the universe.
Note that I’m not making the much stronger claim that this is the best possible use of $20 billion for science. Plausibly a thousand $20-million projects could be found that would advance our understanding of reality by more than a new collider would. But it’s also important to realize that that’s not the question at stake here. When, for example, the US Congress cancelled the Superconducting Supercollider midway through construction—partly, it’s believed, on the basis of opposition from eminent physicists in other subfields, who argued that they could do equally important science for much cheaper—none of the SSC budget, as in 0% of it, ever did end up redirected to those other subfields. In practice, then, the question of “whether a new collider is worth it” is probably best considered in absolute terms, rather than relative to other science projects.
What I found most puzzling, in Sabine’s writings on this subject, was the leap in logic from
- many theorists expected that superpartners, or other new particles besides the Higgs boson, had a good chance of being discovered at the LHC, based on statistical arguments about “natural” parameter values, and
- the basic soundness of naturalness arguments was always open to doubt, and indeed the LHC results to date offer zero support for them, and
- many of the same theorists now want an even bigger collider, and continue to expect new particles to be found, and haven’t sufficiently reckoned with their previous failed predictions, to …
- therefore we shouldn’t build the bigger collider.
How do we get from 1-3 to 4: is the idea that we should punish the errant theorists, by withholding an experiment that they want, in order to deter future wrong predictions? After step 3, it seems to me that Sabine could equally well have gone to: and therefore it’s all the more important that we do build a new collider, in order to establish all the more conclusively that there’s just an energy desert up there—and that I, Sabine, was right to emphasize that possibility, and those other theorists were wrong to downplay it!
Like, I gather that there are independently motivated scenarios where there would be only the Higgs at the LHC scale, and then new stuff at the next energy scale beyond it. And as an unqualified outsider who enjoys talking to friends in particle physics and binge-reading about it, I’d find it hard to assign the totality of those scenarios less than ~20% credence or more than ~80%—certainly if the actual experts don’t either.
And crucially, it’s not as if raising the collision energy is just one arbitrary direction in which to look for new fundamental physics, among a hundred a-priori equally promising directions. Basically, there’s raising the collision energy and then there’s everything else. By raising the energy, you’re not testing one specific idea for physics beyond Standard Model, but a hundred or a thousand ideas in one swoop.
The situation reminds me a little of the quantum computing skeptics who say: scalable QC can never work, in practice and probably even in principle; the mainstream physics community only thinks it can work because of groupthink and hype; therefore, we shouldn’t waste more funds trying to make it work. With the sole, very interesting exception of Gil Kalai, none of the skeptics ever seem to draw what strikes me as an equally logical conclusion: whoa, let’s go full speed ahead with trying to build a scalable QC, because there’s an epochal revolution in physics to be had here—once the experimenters finally see that I was right and the mainstream was wrong, and they start to unravel the reasons why!
Of course, $20 billion is a significant chunk of change, by the standards of science even if not by the standards of random government wastages (like our recent $11 billion shutdown). And ultimately, decisions do need to be made about which experiments are most interesting to pursue with limited resources. And if a future circular collider were built, and if it indeed just found a desert, I think the balance would tilt pretty strongly toward Sabine’s position—that is, toward declining to build an even bigger and more expensive collider after that. If the Patriots drearily won every Superbowl 13-3, year after year after year, eventually no one would watch anymore and the Superbowl would get cancelled (well, maybe that will happen for other reasons…).
But it’s worth remembering that—correct me if I’m wrong—so far there have been no cases in the history of particle physics of massively expanding the energy frontier and finding absolutely nothing new there (i.e., nothing that at least conveyed multiple bits of information, as the Higgs mass did). And while my opinion should count for less than a neutrino mass, just thinking it over a-priori, I keep coming back to the question: before we close the energy frontier for good, shouldn’t there have been at least one unmitigated null result, rather than zero?
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Comment #1 February 4th, 2019 at 8:00 am
You make a good point that any money saved by not building a next collider is very unlikely to be spent on other science projects, but I’d like to know why you think the following logic
applies to the next collider after the LHC and not to LHC itself? It’s not like LHC was the first circular collider ever built, and it’s not like it has found much of anything unexpected. It did find a standard Higgs boson with the modal expected properties and of about the expected mass, and yeah, it’s nice to have definitively detected it, but it was the predicted and expected result, whereas none of the hundreds or thousands of unexpected predictions have panned out. In that sense LHC has already arrived at the desert. So the number of high-level physics information bits gained from it isn’t all that large, in fact it’s quite small, and so Dr. Hossenfelder can feel quite justified in applying your very own logic quoted above at the current step instead of the next one.
Comment #2 February 4th, 2019 at 8:35 am
When you work hard on something you learn something, even if it isn’t what you expected or wanted to find. At worse, it’s an opportunity for people who love science and spent their early life studying it to get paid for science work; in evolutionary terms, for science to survive and reproduce. So I’ll be happy to donate whatever my fair share of the bill is, if someone will point me to a way to.
I’ll also be glad to hear of some other big projects that might compete for the funding, with the bias that if nobody is getting their hands dirty gathering physical data then I’m not going to be sure that it’s real science. (Okay, thinking about the data is also science, but that’s something people like Einstein do whether they’re paid for it or not, and they’re smart enough to get paid doing something else, e.g., Dr. Hossenfelder with her writing.)
Comment #3 February 4th, 2019 at 8:37 am
I agree that we should have one unmitigated null result before we stop looking through the energy frontier. It seems to me that the greatest practical value that a Theory of Everything could have would be in constraining the range of physical phenomena we consider plausible. It’s one thing to say, “We have found no evidence of this particular kind of spooky supernatural phenomena, and all the evidence supporting it is bad”, and it’s another thing to say “Supernatural phenomena of this sort would require dramatic changes to a battle-tested theory of everything that’s been around for a literal century without need of major changes”.
In the former case, the “supernatural” phenomena could exist, and all the investigators trying to prove it could be just bad at their jobs. Maybe it’s all laymen doing it, and they don’t actually know how to prove things. Or maybe there’s a major variable that investigators didn’t control for during their investigation, because they had no idea what possible mechanism could explain the phenomena. Or maybe the question just isn’t scientifically verifiable right now. A battle-tested theory of everything could help if the theory falls into that last category, and maybe with the second.
In the case that it goes against a well-established theory of everything, it’s pretty conclusive that a phenomena is false. Not that people would necessarily stop saying that it’s true, And being able to disprove things conclusively means that it’s easier to find what’s true. Examples of questions that could be disproven are: “Do we have a ‘spirit body’, which affects our mind?”, “Is there any sort of psychic phenomena?”, “Is there anything or anyone with anything that might be described as a ‘spirit body’?”, and “Does dark energy or dark matter do anything that I should know about?”.
Now, right now my understanding is that these questions are not scientific. They’re too broad, and there’s too much of a range of possible mechanisms in them. A theory of everything would narrow down the possibilities, because, as I understand it, that’s what a theory of everything does. It doesn’t tell you anything about what exists directly, since it’s far too complicated to actually calculate for any large-scale phenomena, but it could tell you about what couldn’t possibly be true, set a range of possible answers for how things work, and tell us some cases where approximations we make are likely to fail. Basically, I’m excited for a theory of everything because I’m hoping that it will help people will be able to test “supernatural” phenomena, and I am enthusiastic about the prospect of a new particle accelerator because it would test a theory of everything.
Comment #4 February 4th, 2019 at 8:46 am
“But let’s be honest: It’s disappointing.”, Sabine doesn’t seem to find wrong predictions exciting.
Comment #5 February 4th, 2019 at 8:50 am
So, it’s anti-science to expect the theorists to actually have decent predictions about something before we spend $20b on it, but it’s “robust peer review” when every grant in my field, all of which are literally ~0.002% of the cost (including indirects), has to not only have solid theory, but also preliminary experimental data proving the experiments will work?
Sorry, but I call BS. That money could fund my primary target division at NSF for over 300 years at the current level. Or, more pointedly, they’re asking for over 3x the entire US annual budget for cancer research. Can they really make the claim that the discoveries this device makes will be so much more impactful than researching new cancer treatments?
Look, I love fundamental science; that’s what I do. But I also acknowledge the reality that dropping that kind of cash means you’d better find something and it better be impactful, especially in folk’s day-to-day lives. My work will have only modest effects, none for most people, but I’m literally asking for 0.002% of the cash for experiments that are guaranteed to work (as in “We know phenomenon X exists, but nobody has measured important aspect Y about it, and I’ve invented a tool to measure Y in X.”) So how can people ask for $20b for something without even having strong theories about what it will find or how impactful that will be?
Comment #6 February 4th, 2019 at 9:12 am
Let me fill in the missing steps:
3) many of the same theorists now want an even bigger collider, and continue to expect new particles to be found, and haven’t sufficiently reckoned with their previous failed predictions
4) therefore we do not currently have any good predictions for BSM pheno at a larger collider and no reason to think it will deliver anything but null-results (confirm the SM)
5) but there are other areas where we either have inconsistencies between theory and data or internal inconsistencies in the theories that give rise to good predictions while
6) at the same time, a bigger collider is pretty much the most expensive experiment you can think of (except, possibly, a telescope on the moon), and
7) therefore a bigger collider is, according to the current state of knowledge, not the best investment.
As to the often repeated argument that so far bigger colliders have always found something new, note that so far we have always had missing pieces to look for. This is not the case any more. The SM is complete and it’s fine the way it is. There is no reason to expect anything else before we hit the Planck scale. Unless, that is, you believe in arguments from naturalness, hence their relevance.
Comment #7 February 4th, 2019 at 9:34 am
Candide #1:
So the number of high-level physics information bits gained from it isn’t all that large, in fact it’s quite small, and so Dr. Hossenfelder can feel quite justified in applying your very own logic quoted above at the current step instead of the next one.
One could equally well have argued: if Sabine is right, then why shouldn’t we have applied the same logic even earlier, and declined to build the LHC? After all, the experts were pretty damn sure beforehand that it was going to find the Higgs in such-and-such narrow energy range, and they had no theoretical assurances whatsoever that it was going to find anything else (for good reason, as we know with hindsight). But then, “since that argument is an obvious absurdity, and even Sabine agrees that building the LHC was great, we conclude the next collider should be built as well.” 🙂
This could easily evolve into another abortion debate, where the pro-choice people demand of the pro-life ones, “what principle stops you from declaring that male masturbation is mass murder?” and the pro-life people respond “what principle stops you from legalizing infanticide?”
In both debates, I’d say that any of us whose position is “more than zero and less than infinity” had better give up on logical deduction to the right answer, and settle for (1) distinguishing the good arguments from the bad/irrelevant ones, (2) looking for guidelines that approximately capture the relevant intuitions, and then (3) making a judgment call.
Comment #8 February 4th, 2019 at 9:51 am
Supporting a massively expensive public works project, scientific or other offers a politician little to no additional political capital among the general public if the project is successful, sometimes many terms after their role in supporting it (whose campaign was helped by LHC, LIGO etc. ?) and exposes them to political risk if the project can be even remotely credibly cast as a failure or waste by detractors long before its completion.
I suspect the reasons projects of that kind ever got funded were either the cold war era where bloc one-upmanship was itself politically selling or because the political support of large-impact groups such as industry lobbies, labour unions and the academic establishment could be effectively collateralized in return.
In either case the underlying scientific merit probably never played a deciding role (space shuttle program anyone ?).
Which isn’t to say that the people with actual interest in the underlying questions shouldn’t be debating it or thinking of better alternatives for the proposed sums.
Comment #9 February 4th, 2019 at 10:19 am
There are two outstanding mysteries in physics today, dark matter and dark energy. If we can spend 20-30 gigabucks on experiments, it might be nice if they can address those mysteries.
Comment #10 February 4th, 2019 at 10:27 am
Scott, re funding, obviously this is correct “none of the SSC budget, as in 0% of it, ever did end up redirected to those other subfields”
There’s another aspect of funding though that we need to take into account. Funding a big project confers status. Intellectual status. So if you spend $20B on something, then the field will align to self justify it. That’s a true, if perhaps unpleasant, aspect of human nature that I don’t think anyone can deny.
So the social impact to science should be taken into account as well. Even if the $20B would not be pulled from other budgets, the arguement must still be made is this the correct subfield of science to be given $20B of prestige too? If Sabine is correct, then the answer is no. In fact, it’s sort of a shame that the price tag is so big. Because if it were far less, then it would be clear the funding should be given since it would not warp the field, and people could go find out.
In short, even if the funding comes for “free” in the sense that not funding means the money goes away, we have to consider the side effects of indirect endorsement when something so large gets the prestige of funding.
Comment #11 February 4th, 2019 at 10:28 am
Scott #7:
Indeed. Arguably we should have. However, contra #8, academic/high-tech jobs programs do generate political capital via the usual porcine-equine-arboreal mechanisms, not to mention the threat of being tarred as anti-science, and were it not for the extremely polarized and volatile political climate that currently prevails, I’m fairly certain that some kind of next-generation collider project would get funded. In fact I give it better than 50:50 chance even as it is.
As for the debate evolving as you suggest, I doubt that, because while almost everyone cares quite strongly about kids and reproductive rights one way or another, vanishingly few people care at similar levels of intensity about elementary particles. It could have been different in an early Soviet-type ideological environment when the stakes were way higher than not having grant money in addition to your tenured salary, but in the current environment in fields far from crimethink-rich areas I suspect that the tendency to go along to get along keeps academic/bureaucratic infighting at a fairly low level. It certainly jibes with what I observe in my little corner of it.
Comment #12 February 4th, 2019 at 10:40 am
“if civilization could get its act together and find the money, I think it would be pretty awesome to build a new collider “. Civilizations don’t ‘find’ money. Governments tax (i.e. steal – take without consent under threat of punishment) its members. At the very least, there should be a referendum where taxpayers express where they want their money to go but the best solution would be libertarian; it would be for voluntary contributions to be made to fund construction of a collider.
Comment #13 February 4th, 2019 at 10:48 am
To try to find the crux in the Scott/Sabine honest disagreement:
Scott talks about efficient use of resources: in Physics funding mega projects get the funding otherwise not available, not sucking it from the smaller projects (cue SSC, well, the other SSC), and raising energy would either find something new and exciting (admittedly with low probability) or force some serious self-evaluation among the HEP crowd.
Sabine points at the groupthink in the HEP community, and how the proposed FCC and the ostensible rationale behind it is wishful thinking and a PR lie, and a manifestation of the diseased community, sort of like bigger and bigger Easter Island statues. Building the collider would delay addressing this disease for decades to come. Unlike the Superbowl, which happens every year, new results or non-results would have to wait for a long long time.
The other SSC would probably frame this as a high-energy collision between Mistake Theorists (Scott’s view of the HEP community) vs Conflict Theorists masquerading as Mistake Theorists (Sabine’s view). I’m looking forward to a new grain of truth being discovered after a few runs.
Comment #14 February 4th, 2019 at 11:12 am
Scott says “Plausibly a thousand $20-million projects could be found that would advance our understanding of reality by more than a new collider would. ” I think this an enormous understatement. I’d defy you to identify ANY collection of 1000 different $20M experiments that anyone would ever fund that would give you less understanding. Just limited to basic physics, such experiments would surely include attempts to understand limits of quantum computation, high temperature superconductivity, 2D and nearly 2D systems such as graphene, understanding pulsars, megnetars and FRBs, trying to find dark energy and dark matter, etc. Tool-building would contribute indirectly (atom interferometers, plasma wave accelerators, etc). And if you include other fields such as biology, the number of informative $20M projects is even greater. A portfolio of small and medium sized projects would surely be a better bet.
Comment #15 February 4th, 2019 at 11:22 am
There is a parallel with this argument and one from the DWave arguments. Scott, you had a basic worry that DWave hype not matching reality would eventually poison the well as it were for other quantum researchers by making it seem like all this “quantum” funding was just money down the drain.
Likewise, many very lofty things are said (borderline, promised) about a new bigger collider. What is the political effect on funding across the field if this tremendously expensive investment proves to be a failure. I think Sabine’s position that “insiders” should at least be honest with the public that a larger collidor is gamble hoping that something is found.
Comment #16 February 4th, 2019 at 11:25 am
Also
Not funding one order of magnitude larger collider today does not necessarily mean closing the energy frontier for good, the idea can be revisited after a few decades of progress in physics, engineering economics and politics have taken place, and if by then we’re all too busy scavenging for food and hiding from AI-controlled killer robots knowing that we have experimental evidence for supersymmetric partners will probably offer little comfort anyway.
Wouldn’t the same logic apply to the LHC ? Probably yes, even most scientifically-minded people would be just as fine living knowing that the Higgs boson is somewhere in that range and we’ll get around to confirming it at some point – this is why it was important to frame the LHC as experimentally validating the underpinnings of the standard model and thereby all of modern physics, calling it the “god particle” etc. If something similarly grandiose can be credibly said about a potential discovery in the energy scope of the new proposed collider it would probably help its case a lot (which afaic is what Sabine is saying)
Comment #17 February 4th, 2019 at 11:47 am
#13
Oh no, not at all. Scott’s point, with which I agree, is that if a big scientific project is not funded, the equivalent money isn’t spent on other scientific projects but rather on non-scientific things (“pornography, sugar water and bombs”, as Neal Stephenson put it). But the converse is not true: smaller projects can and do get starved of funds and sucked out by big projects in related subfields. This occurs e.g. in fusion, where most everybody who works on magnetic confinement tries to hitch their wagon to ITER and those who can’t have a choice of languishing in penurious obscurity or selling vaporware to gullible investors. (I exaggerate slightly for emphasis.)
Comment #18 February 4th, 2019 at 11:53 am
I don’t buy the argument that the worth of a new collider should be consider entirely on absolute terms. I used to work in astrophysics and there the competition between megaprojects and smaller ones is very clear (and indeed, IIRC the most recent decadal survey emphasised the balance between projects of different sizes). I find it very hard to believe that the money for a new $20 billion collider would come entirely in addition to other funding, without hurting smaller projects.
Comment #19 February 4th, 2019 at 12:01 pm
Would be useful to estimate how much LHC and the next collider contribute to the happiness of society in present and future (surely there are, or going to be soon, some KPIs for happiness, it’s a fasionable topic these days). Then make a similar estimation assuming that 20 billion is spent on quantum computers… or other things, you name it. I’m sure that not knowing whether the Higgs boson exists would not prevent most people from living a happy and fulfilling life. This does not mean I disapprove scientific research, but 20 billion feels a bit of an overkill. The only justification I could imagine is national security, however, LHC is an international collaboration.
Comment #20 February 4th, 2019 at 12:49 pm
#14: I was going to make a related point: Parkinson’s bike-shed principle says that the cost of selling a scientific project (in time, money, reputation, political capital, whatever) grow nowhere near linearly with the cost of the project. This naturally favors concentration of funding into big mega-projects to the detriment of overall efficiency. A relatively well-established way of avoiding this problem has been the creation of dedicated funding agencies such as the National Cancer Institute, but they are subject to the same incentives in addition to the normal bureaucratic incentives of post-WWII, Vannevar Bush-style official science, so it doesn’t help much in the mid-to-long term.
Comment #21 February 4th, 2019 at 1:34 pm
Hi Sabine #7 — in your step 3, can you be a bit more specific about what “sufficient reckoning” would entail? And can you be a bit more specific about your step 5? What predictions ought we be testing?
Comment #22 February 4th, 2019 at 1:59 pm
General relativity is not complete. There is no desert.
Comment #23 February 4th, 2019 at 2:11 pm
People try to assess the future by asking questions, whether or not a bigger collider will solve the current mysteries of physics? It’s easy, because no one knows the answer. It’s just opinion. Possibly they should better ask themselves, if they would like to live in the world today, if it where not for our ancestors to have spent much bigger sums on technology with the same risk of getting out nothing of it? I regard it as a kind of decadence and double standard when people who profit(ed) the most from modern technology preach to lessen its potential impact for future generations. Taxpayers money is wasted in gigantic amounts for military purposes, but almost no one complains. If something meaningful shall be done with it, instead, the mourning starts. Sometimes I doubt why anyone should do anything to improve the lives of his fellow human beings, when there is not even a little appreciation for the things science and technology has done for all of us so far? And this appreciation is shown by society by paying the bill for the future collider after experts have found it reasonable to build it, on the basis of their consideration of the technical and theoretical terms, but not based on sociology, majority referendums, ill-informed minority viewpoints, or, worst of it, ideology.
Comment #24 February 4th, 2019 at 2:25 pm
From 49:00 to 59:00 David Tong offers a sympathetic-to-all summary that concludes with a personal view that is worthy of consideration, and that sort of supports Sabine’s argument by suggesting going back to the drawing board to search for evidence that might challenge assumptions. He doesn’t support her strong position that the machine should not be built, but presents an alternative https://www.youtube.com/watch?v=zNVQfWC_evg
Comment #25 February 4th, 2019 at 2:39 pm
There is something funny about theorists who have probably never performed an experiment in their lives trying to deside the fate of experimental physics. And using the most facile of arguments – they won’t find anything new. Many experiments do not find anything new, that does not mean that the confirmation of our current theories at greater precision is somehow worthless. There is a lot of things we still do not understand about they Standard Model. At greater energies we can better explore quark-gluon plasmas, various aspects of the weak interaction, you name it. That is the purpose of instrumentation – to help you explore a physical domain. Can we quit it with the infantile view that science is only about ‘dicovering’ big cool things.
Comment #26 February 4th, 2019 at 2:51 pm
I have to admit that the level of economic illiteracy on this topic is astounding. You’d think people would learn the difference between a national economy and a household one, and why the two are not the same.
The other problem is everyone thinking that this is just a sunk cost. Such ignorance on a science blog worries me. CERN has been a major employer of not just physicists, but many tecnicians and engineers. It has had to work closely with many European industries to develop magnets, lasers, optics, computers, and so on, that it required. Good high tech Keynesian stimulation. A lot better than the American military-industrial stimulation if you ask me. Who wants to put a value to the World Wide Web or Grid Computing?
Then there is the fact that you are also creating a wonderful international community. Opening up educational opportunities, and allowing large amounts of cross-fertilization between different areas of physics. It’s not all about particle physics, J.S Bell worked at CERN. The idea that 20 billion over what is it, 10-20 years, is somehow not worth it is such an incredibly shallow viewpoint.
Comment #27 February 4th, 2019 at 3:01 pm
YesIHaveAName:
‘Not funding one order of magnitude larger collider today does not necessarily mean closing the energy frontier for good, the idea can be revisited after a few decades of progress in physics,’
No, thats the problem, it cannot be revisted after a few decades. Large scale, complex projects like CERN or the Space Program require an experienced army of technicians, engineers and scientists who have expertise in many relevant areas. Without any support, these people will just grow old and disappear. Young people will keep away from these areas since they can’t see any future in it. How will you plan to restart this research? You will need to wait a generation just to train the required personnel. The cost of starting from scratch will be significantly greater too. No, if you you no longer try to grow high energy physics via incremental improvements, it will disappear for good.
Comment #28 February 4th, 2019 at 3:07 pm
Shawn #22: The “energy desert” is generally defined as a hypothesized enormous-but-finite region where nothing happens, in between the current electroweak scale and the scale where something new had better happen—namely, the Planck scale (i.e., that of quantum gravity / GR), or perhaps the GUT scale. Alas, the gravity oasis at the other end of the desert seems out of reach without astronomically large accelerators.
Comment #29 February 4th, 2019 at 3:13 pm
Bunsen Burner #25-27: As a warning, all remarks of the form “I’m astounded by the illiteracy / ignorance of the other commenters” violate my comment policy and risk a ban.
In reply to YesIHaveAName #16, though, I was also going to write that engineering traditions passed down across the generations (like building accelerators) are incredibly hard to restart from scratch. With manned space travel and nuclear weapons design, to take two examples, it seems plausible that civilization has not only not progressed much in the last half-century but lost much of the expertise that it once had—though in both cases, to different extents and for different reasons, it’s not obvious to what extent that should be mourned.
Comment #30 February 4th, 2019 at 3:15 pm
Tamás #19: I’m going to ballpark that the discovery of the Higgs increased global bliss by roughly 125 smileyons, or one per GeV.
Comment #31 February 4th, 2019 at 3:24 pm
Point taken Scott. I was just venting out of general frustration, it was not a comment directed at anyone in particular
Comment #32 February 4th, 2019 at 3:53 pm
Scott,
I believe that if gravity is quantized, then flooding an object with gravitons will cause the object to respond in kind, in spite of the object’s default tendency to scatter gravitons omnidirectionally. If one compactifies the gravitational field down into a gravitational beam, then the gravitons are not being scattered omnidirectionally at all. On the way down from a 3+1D field to a 2+1D disk, to a 1+1D beam, the strength of the gravitational interaction increases by the factor c^2. The desert is not a desert, and the interactions lie on a logarithmic energy scale. Speaking of astronomically large, so are galaxies and filaments. Is dark matter a quantum effect mixed with nonlinear feedback?
Comment #33 February 4th, 2019 at 4:01 pm
Scott #29-30: Don’t ban Bunsen Burner, he has a very good point, the positive potential “side-effects” may be the strongest argument for the next collider (who cares about the Higgs boson if we have World Wide Web as byproduct?). And thanks for your ballpark estimation, very efficient way to convince people with economic illiteracy like myself 🙂
So what do you think has the bigger chance to give us something revolutionary (expected or unexpected) like the World Wide Web: $20 billion more for QC or $20 billion for the next collider?
Comment #34 February 4th, 2019 at 5:11 pm
Tamás #33:
So what do you think has the bigger chance to give us something revolutionary (expected or unexpected) like the World Wide Web: $20 billion more for QC or $20 billion for the next collider?
$20 billion for quantum complexity theory in particular, especially oracle separations. 🙂
Comment #35 February 4th, 2019 at 5:28 pm
Michael Musson #15:
There is a parallel with this argument and one from the DWave arguments.
Yes, I guess the parallel involves hype, amplified via press releases—about observing mini black holes or extra dimensions in the one case, or about getting huge speedups for NP-complete problems in the other. (Though I don’t think anyone ever claimed to have already seen signatures of mini black holes or extra dimensions, which breaks the analogy somewhat.)
I think the right response to irresponsible hype is to correct it, and thereby raise the cost of indulging in it—as I’ve tried to do on my blog with outlandish QC claims, and as Sabine and Peter Woit have done on theirs with outlandish HEP claims.
The question of what engineering projects should or shouldn’t be undertaken is a separate one. Hype is just a distraction to that question. I oppose linking the two questions, either by letting hype drive engineering decisions, or by deciding not to pursue a project as a way of “punishing” hype.
As I said many times about D-Wave, I have no particular objection to (in that case) private investors pursuing some high-risk approach to noisy quantum annealing, once the issue of hype has been removed.
Sabine, by contrast, has now taken a clear stand not merely against irresponsible hype, but against the actual building of a new circular collider itself, and has taken her case to the public—so it’s natural that physicists are responding to the latter.
Comment #36 February 4th, 2019 at 5:43 pm
The greatest thing about this debate is that it is driven by absolutley no tenured professors of physics.
One of the problems, in the age of blogs and twitter, is that getting tenure takes up a lot of time, and one thus doesnt have time to participate in social media.
So it is that science policy will be driven by those who, to put it bluntly, failed at the higher levels of science.
Comment #37 February 4th, 2019 at 5:53 pm
MCA #5, Sabine #6, Lou Scheffer #14, others: I guess one’s feelings about a new collider largely depend on how much one accepts the premise that “smashing particles into each other harder and harder to see what comes out” is not just another example of a physics experiment that one can do, but in some sense is “the universal fundamental physics experiment”—the way you query the universe about what it’s doing at smaller and smaller scales. Like, I could imagine a scenario wherein, whenever two alien civilizations first establish radio contact with each other, the way they figure out which one is more advanced is by asking each other two questions:
(1) how many Mersenne primes have you found?
(2) what energy scale have you reached in particle physics? 🙂
Or maybe that’s wrong, and both quests are just products of temporary ignorance (certainly the first will become quite boring, if and when the infinitude and distribution of the Mersenne primes is ever rigorously proved).
Sabine, it seems like an absolutely crucial part of your case that you think there are other, cheaper and more valuable fundamental physics experiments that could be done instead—and I might need to read your book to learn what they are! Let’s set aside better testing of QM itself, which I know a little about, and which will happen, if nothing else as a byproduct of large investments in quantum information. Besides that, OK, there’s astrophysics (including ultra-high-energy cosmic ray detectors), cosmology (still looking for B-modes?), dark matter searches, precision neutrino experiments (e.g. to learn whether neutrinos are Majorana), all of which have indeed been pursued, though probably less than they should be … and what else?
Comment #38 February 4th, 2019 at 6:03 pm
Sarah Goldstein #36: Your comment doesn’t make sense to me. If someone already has tenure, then can’t they in principle spend plenty of time on social media? 🙂 If they don’t, it’s because they choose not to.
For the record, Jeremy Bernstein and Lisa Randall do have tenure in physics, and Daniel Harlow surely will soon. (Many, many other tenured physicists are obviously participating in this discussion although less publicly.) I have tenure in CS, with a courtesy appointment where I can supervise physics PhD students. I never sought tenure in physics.
Comment #39 February 4th, 2019 at 6:10 pm
Ed #9:
There are two outstanding mysteries in physics today, dark matter and dark energy. If we can spend 20-30 gigabucks on experiments, it might be nice if they can address those mysteries.
Those aren’t the only two mysteries, but indeed, I understand that one of the central hopes for a post-LHC circular collider is precisely that it might find dark matter candidates. (From a talk by Nima Arkami-Hamed, I learned that a major reason why theorists were disappointed by the “downgrade” in energy, in going from the SSC to the LHC, was that it put some plausible dark matter candidates out of reach.) Likewise, one can hope that pretty much any advance in fundamental physics will shed new light on dark energy.
Neither is even close to guaranteed, though. As Sabine points out, it’s consistent with current knowledge that there could be absolutely nothing new to be discovered from here all the way up to nearly the Planck scale—which itself would be a remarkable fact.
Comment #40 February 4th, 2019 at 6:29 pm
The best question that I can think of is: what is the number of gravitons emitted by a 1kg mass per second? I don’t believe that there’s an answer as of today.
Comment #41 February 4th, 2019 at 6:50 pm
I’m not a physicist. I am a skeptical person. For me, both the experimental confirmation of the Higgs boson, and the experimental confirmation of the gravitational waves were important achievements. Therefore I am a bit unhappy if LHC is described as a failure, just because it didn’t find much else beyond the Higgs boson. In both cases, I was initially a bit skeptical whether the data analysis was really good enough, but later decided that the evidence in favor of the discoveries was strong enough.
What about null-results, like (Super-)KamiokaNDE ruling out proton decay? Are those important achievements? Maybe, but the initial goal was not a null-results, and the Nobel price was awarded for the work on neutrino oscillations, not for ruling out proton decay. For me as a skeptical person, a null-result is more convincing if the researchers really tried hard to find something, as opposed to the initial goal already being a null result.
I understand Bunsen Burner’s arguments, and similar arguments already initially made me sympathetic towards the new collider. But my arguments were worse, like building the new collider to find out whether SCC would have found anything interesting or not. On the other hand, if I am honest, I would probably not care either way, independent of whether the new collider would find new physics or not. For quantum computing on the other hand, I would be thrilled by both confirmation that scaleable quantum computing is possible, and also by the opposite result that it is impossible.
Comment #42 February 4th, 2019 at 8:19 pm
Scott #37: I agree that high energy particle physics is indeed very fundamental, and I’m not suggesting just forgetting about it. But spending a lot of money on it right now is like doing a depth first search in a tiny corner of parameter space. You’d get a lot more bang for your buck with a breadth-first search, doing 1000 experiments in as many areas of the boundaries of physics as possible. Then pursue particle physics once you have tried the lower cost options.
In many ways this is a Bayesian argument. We should perhaps estimate the odds of finding something new times the value of that finding. Some may find super-fundamentals to be of immense value, and hence worthy despite low odds of success. Others, myself included, think better understanding of quantum computing, condensed matter physics, etc. are at least as valuable, and as they are much lower cost to investigate they are preferable. You can take this further with research into topics such as gut-biome interaction with mammal physiology. It’s about as far from fundamental as you can get, but far more likely to produce “useful” results. I’d take it over a new collider.
Sarah Goldstein #36: I think you’ve got this backwards. The value of a debate like this comes from the variety of backgrounds of the participants. In contrast, the contribution of tenured particle-physics professors has literally zero information content, since you know what they will think of funding more research into particle physics before they even begin to speak. And while your general point of priorities being decided by those who have “failed at the higher levels of science” could be true, this blog in particular contains many folks who have succeeded at the highest levels of science, just not particle physics. And if you consider intellectual reciprocity, I suspect the knowledge of particle physics by the average contributor here exceeds the knowledge of the average particle-physics person in the specialty of the commenter.
Comment #43 February 4th, 2019 at 8:59 pm
Shawn #40: Unless I’m mistaken, an isolated inertial mass wouldn’t emit any gravitons at all, just like a non-accelerating electric charge doesn’t emit any photons. Hypothetically, gravitational waves could be seen as composed of gravitons, and also, gravitational interaction between multiple masses could be seen as mediated by the exchange of virtual gravitons. (Corrections welcome.)
Comment #44 February 4th, 2019 at 9:12 pm
“After step 3, it seems to me that Sabine could equally well have gone to: and therefore it’s all the more important that we do build a new collider, in order to establish all the more conclusively that there’s just an energy desert up there—and that I, Sabine, was right to emphasize that possibility, and those other theorists were wrong to downplay it!”
The problem with this rationale is that the individuals (or their heirs) who wish now to build the Super-Duper Collider would, upon observing that “nothing was delivered,” simply turn around and say, “But that’s only because we made a silly mistake: we didn’t scale up to sufficiently high energies. So actually, this demonstrates the need to build an even bigger one now. We regret having set our sights too low, but after all, physics is an experimental science, and we have learned…”, (etc.).
I cannot imagine a socio-rhetorical universe in which this would not happen.
Comment #45 February 4th, 2019 at 9:34 pm
I think Sabine has the better part of this argument and you do not do her reasoning justice. There is no big leap from 3 to 4. Sabine is very clear that she thinks the onus should be on particle physicists to give theoretical motivation for spending $20 billion. So far she claims they’ve responded with bupkis. That is, the only all of their predictions are based on the same unsound motivations. I have yet to see anyone actually rebut this or take her horn.
Exploring the Higgs and fully mapping it out may well be a good way to spend $20 billion, but few have been willing to stand up and say, “You are right Sabine, we have no sound motivation to expect we will see anything else, but we should still do it to map out the Higgs!”
Instead, we get evasion and muddying the waters and a general unwillingness to either rebut her and claim there is sound motivation OR acknowledge she is right and we should spend it anyway.
Disappointed.
Comment #46 February 4th, 2019 at 9:59 pm
Scott says,
“Neither is even close to guaranteed”
VS
“it’s consistent with current knowledge that there could be absolutely nothing new to be discovered”
I would humbly suggest that there is a bigger gap here than between Sabine’s three and four. Even the latter formulation above has the misleading “could” doing some heavy lifting.
Comment #47 February 4th, 2019 at 10:01 pm
Atreat #45: You can agree or not, but I thought people were pretty clear and consistent that the motivation for building a larger collider is to find out whatever is there at the next higher energy scale—the same, basically, as the motivation for sailing further out into the Pacific than anyone has yet sailed, in search of new continents or islands, which might well exist despite some people having given bad arguments for their existence. (E.g., I recently learned that European explorers were inspired to reach Australia and later Antarctica, in part because of a then-popular theory holding that there had to be a great Southern continent to “balance” the Northern continents.) Today the earth’s surface has been fully mapped down to the individual buildings in Google Street View, but at least the energy frontier beyond the electroweak scale remains totally open and unexplored—thar be dragons, or maybe just thar be a huge ocean.
Comment #48 February 4th, 2019 at 10:06 pm
Atreat #46: Wtf? Not only are those two statements manifestly consistent, they say much the same thing!
Comment #49 February 4th, 2019 at 10:15 pm
Scott #47,
No, that is manifestly not true. They are claiming that we have good reason to hope that we *will* see something and then get evasive and unclear as so as you ask them what we will or see or *why* there is good reason. People don’t generally embark on journeys of discovery without hope. And when you ask them what gives energy to their hope they generally share it. Here we have hope and an unwillingness to acknowledge failure of the same motivation that powers that hope. All of this is very damaging to public trust in science and scientists as fair minded and rationale – the best of us – and betrays a bunch of motivated reasoning based on selfish and personal biases.
$20 billion *is* a lot of money and it is ironic that scientists and rationalists would pray on human weakness for understanding large numbers to claim it is just a drop in the bucket. There is a hell of an opportunity cost with this.
Acknowledge or rebut the claim that Sabine makes that there exist no sound motivation to expect to see anything new beyond mapping out the Higgs sector. Then based on that tell us if you would spend the money anyway and why the opportunity cost should be paid. That is the honest way to respond to the Sabine’s gauntlet.
Comment #50 February 4th, 2019 at 10:18 pm
I read them as, “No, we can’t *guarantee* that we will find something, but we have excellent reasons to hope we will!” vs “Our current knowledge predicts we won’t find anything…” you don’t see a gap with that???!!!
Comment #51 February 4th, 2019 at 10:26 pm
It is simple Scott: do you personally know of any good sound theoretically justified reasons for thinking we will find something new beyond mapping the Higgs? Yes or no?
If you don’t personally know of any… do you have high confidence in someone else who purports to have such? Yes or no?
If not, then why should we spend $20 billion and pay the opportunity cost without any good sound reasons beyond nebulous and unmotivated hope? If the answer is we should map the Higgs sector and that alone is worth the cost… well, I am sympathetic, but failure to answer the first questions or dance around them makes me queasy.
Comment #52 February 4th, 2019 at 10:48 pm
Bunsen Burner #27, Scott #29
Unless everything about the currently targeted energy scale has been exhausted, not funding a new collider should not imply shutting down CERN and the field of high energy physics altogether either.
Re. the proposed project being a case of Keynesian stimulation that is just another way of asking what the best use of 20 billion public dollars is, in fact it is those economical side benefits that would end up dominating the decision making process as per my first comment.
It is probably unavoidable that some expertise would be lost and have to be regained but that could be a case of Keynesian stimulation by itself as it would hopefully be done in light of new goals and technologies just like the current progress allegedly taking place in space exploration.
Comment #53 February 5th, 2019 at 12:10 am
Well, didn’t Hossenfelder originally predict in a blog comment that the LHC would find nothing new at all, not even the Higgs? Having trouble finding this using Google (maybe a reader here can help), but distinctly remember reading Lubos Motl explain to her in the comment thread why this was impossible. If so, she’s in no position to criticize.
Comment #54 February 5th, 2019 at 12:29 am
In my opinion, Bee is right. If you are going to spend $20 billion on an experiment, you have to have some good reason about what you might discover. All we have been given is a hope that at higher energy levels we might find SUSY particles we haven’t found at current energy levels, or maybe something else. No one has provided any cogent reason that we should discover anything at all, except a desert. Imagine a lowly researcher requesting research money with the reason “I might discover something with this experiment.” She’d get a horse laugh as her reply.
Comment #55 February 5th, 2019 at 1:39 am
Scott #34: I agree. There is a low-energy way of exhibiting the Higgs boson: just run the (Higgs) boson sampling algorithm on a quantum computer. Now, if the sample we get happens to be empty, we conclude that the Higgs boson does not exist. Easy. (Will you ban me now?)
Comment #56 February 5th, 2019 at 2:33 am
Dr. Sarah Goldstein:
I think there is an element of truth to what you say that scientists are often uncomfortable expressing. However, I would modify your assertion about tenure. It’s not tenure that’s driving this debate, but participation in research. Scientists engaed in research simply have far more limited time to engage with people via blogging. You’ll notice that when Scott is producing a paper or away at a conference, this blog remains empty. Trying to do high level research and entertain people on your blog is too exhausting. However, if you’re a contrarian blogger with no research to worry about, you can fill the internet with your thoughts on a daily basis. I have friends at CERN who could provide fascinating exposition on how little we understand the Standard Model. How their research can help us better understand the nucleus, or help astophysicists model exotic states of matter. Unfortunately, they don’t have the time. They work 12 hour days, and whatever free time they have left is family time.
Comment #57 February 5th, 2019 at 5:31 am
I am a retired particle physicist active with experiments at CERN since the late sixties. This discussion confuses two issues, “money” and “knowledge”.
When money was spent in Europe after the war to build CERN , there were no models of anything. The top nuclear physicists of that time used “look at the atom bomb that came out of nuclear research, maybe we find something as good at higher energies”, and remember that was the cold war time. So the argument was not physics.
Then when we started discovering symmetries in the experimental results the whole theoretical subject took off, with beautiful models and mathematics, and when the LHC was proposed theoretical expectations were high .There is a large theoretical community of physicists now that is interested for learning further , and the monetary and applications implications are not really addressed in the discussions.
Nevertheless, in this link
https://indico.cern.ch/event/398256/attachments/798707/1094710/CERN_slides_v_4.pdf
there is a cost/benefit analysis of the LHC, where the probability of society getting back the cost is at 95% , without counting in extra technological gains for society.
It is about these extra technological advances that LHC brought that I would like some numbers for . I.e. what is the value added to the Gross World Product by the invention of the world wide web? The GWP is in trillions, and the fact that we communicate on this blog is based on that ingenious discovery . At the time there were four experiments at LEP each consisting of about 12 university groups in disparate geographic locations . The pressure for fast communication in the analysis was great. No such pressure existed at the time outside the high energy demands. The same is true for LHC large data banks and communication and distributed processing with the demands an order of magnitude higher in group structures. Also the building itself with the superconducting magnets advanced the technology.
So the money return of the LHC is a multiple , maybe even huge multiple , it needs a study by economists.
In this sense, building the FCC and (any higher energy colliders) will certainly push technology a stage higher, and who can predict the benefits for society, except in analogy?
Certainly particle physicists want to cross the next frontier hoping for something exciting and will defend it as the advancement of knowledge at the frontiers crossed.
The argument against the physics proposition reminds me of :
“There is nothing new to be discovered in physics now. All that remains is more and more precise measurement.”
Attributed to Lord Kelvin and some others before him. History showed how flowed this argument was.
I could go on with surprises that could result from finding the large extra dimensions of some string models ( it was what I was thinking about at the time I retired in 2000), to science fiction results from the physics that will be studied at higher collider energies but will stop here.
Comment #58 February 5th, 2019 at 6:04 am
My problem is that at that big a scale, I have no intuition at all for which projects costs how much, or what other projects could 20 giga dollars fund. Without such information, it’s pretty hard to tell which big efforts are worth to spend on.
Comment #59 February 5th, 2019 at 6:47 am
Scott #43 You are correct in the general relativity framework. A single charge does not radiate unless accelerated. and the same would be true for gravitational waves with the caveat that the inertial mass should be asymmetric for a gravitational wave to be generated.
At the quantum level, one should remember that atoms and molecules generate black body radiation due to the rotational and vibrational degrees of freedom, by local accelerations in each others spill over field. This would be more complicated for quantized gravity, as gravitons are emitted by acceleration of asymmetric distributions , due to their spin 2, thus very low probability even ignoring the tiny gravitational coupling.
Comment #60 February 5th, 2019 at 7:34 am
Global debt is around 200 trillion. What’s 20 billion for an experiment? Nothing. If somebody has other experiments to propose, go on influence and propose them.
Comment #61 February 5th, 2019 at 8:19 am
Tamás #55: No, there’s no ban for terrible and pointless albeit inoffensive jokes. 😀
Comment #62 February 5th, 2019 at 8:54 am
At the end of the day, almost every scientists will agree it’s not the best possible use of $20 billions for science. Let’s set a competition and fund better projects.
(Yeah, I’ve read the argument that none of SSC money went to other research. That’s not a reason to advocate a bad project. That’s a reason to work through international collaborations rather than rely on the idea that the US congress will work properly.)
Comment #63 February 5th, 2019 at 9:11 am
Thanks for the information!
Comment #64 February 5th, 2019 at 10:04 am
Anna V #57: You say “It is about these extra technological advances that LHC brought that I would like some numbers for . I.e. what is the value added to the Gross World Product by the invention of the world wide web?”
You can’t count the whole Web as a benefit of LHC. It almost surely would have been invented by someone else had not LHC done it – the idea was well known since the days of Xerox Parc. So the LHC credit is the opportunity cost saved by starting a year or two earlier. This is likely a positive contribution, but a much smaller one.
If the Wright brothers had not invented their airplane, it’s not like we’d have no airplanes at all. It’s not even clear the state of the art would be behind where it is now – had they not existed, whoever *did* invent it might have built a more forward-looking solution.
Comment #65 February 5th, 2019 at 11:01 am
Anna V #57: Sorry for being the devil’s advocate, but thinking back to the time I was young, especially childhood, I’m not sure at all whether the world wide web would have made me any happier. Sure, the GDP, the economists… for me the question is would it have been so terrible if www comes some decades later? Again, I’m only sure that knowledgeable people could list both pros and cons endlessly (including science but also other aspects) and in the end everbody would just believe whatever he/she wants, if anything. I doubt there is a conclusive yes/no answer here.
Comment #66 February 5th, 2019 at 11:53 am
Tamás #65: I hereby give you credit for the most original argument in this thread so far. “Sure, CERN deserves credit for having invented the web … but has the web really and truly made us happier?” 😀
Comment #67 February 5th, 2019 at 12:01 pm
Atreat #49-#51: I hate to say this, given that I value our friendship IRL—but the hectoring tone of your comments, and the constant imputations of intellectual dishonesty on the part of me and anyone else who disagrees with you and Sabine, are in violation of my comment policy.
Here’s what I can say: among the smartest and most accomplished particle physicists who I know, I don’t think any of them would ascribe less than a ~30% probability to the discovery of new physics from a 100TeV circular collider, although it might be like pulling teeth to extract such a number. The central argument is that so far, there always has been new physics when you explored at higher energies, and some of it (e.g., the muon and tau) had no known theoretical reason to be there beforehand—it was just there. And we know that something has to be the dark matter, and something has to be responsible for the neutrino masses, and so on. And in principle, you could push everything new all the way up to the Planck energy, but why make that maximally pessimistic assumption if we’ve barely even started to look?
So, given that any new physics would probably be several dozen bits of new information (e.g., the masses and properties of the new particles), in expectation, there’s probably at least a half-dozen bits of new information about the universe to be had! Now, $20 billion might sound like a lot to learn a half-dozen bits … but think about it this way, how much would you pay to learn a half-dozen bits from God? 😀
Comment #68 February 5th, 2019 at 12:18 pm
Lou Scheffer #64: I think there’s a strong case to be made that, had Berners-Lee not invented the web, whatever arose instead of it would probably have been more proprietary, centralized, and worse. (Remember when Prodigy, AOL, and cable modems were going to be the future? I was only an adolescent at the time, but I do. 🙂 )
Comment #69 February 5th, 2019 at 12:30 pm
Hi Scott,
I *have* taken a strident tone and apologize if it has crossed the line into bullying. I’m just dismayed and disappointed so commenting out of some distress. I have *no doubt* that if you polled the world’s leading particle physicists they *would* come up with such an optimistic probability and more’s the pity.
You say the central argument is that “there always has been new physics when you explored at higher energies”, but I don’t think that is their argument at all. First of all, “new physics” is ambiguous here. It could mean just mapping out the Higgs or it could mean they *expect* to find new *predicted* particles. To my knowledge, the only people who are claiming the latter are those who continue to develop theories motivated by the failed naturalness arguments Sabine wrote a book about. These are entirely two different things. Another possible meaning is that they expect to find the unexpected.
The problem I am having is that there is a lack of clarity on the part of those responding to Sabine and pushing for a new collider. Some *are* clear in that they admit that only mapping the Higgs is *expected* new info and that we should do it anyway and kudos to them. Others don’t wish to admit failure for the failed lines of reasoning or other failed motivations for bad predictions and are just clouding their response using an all-of-the-above approach. That’s not you, but I think it might be an apt description of some of your friends.
Comment #70 February 5th, 2019 at 1:46 pm
Hi Scott,
I would try to suspend two equal masses (say, 1kg each) in the Earth’s gravitational field.
I believe that the gravitational time dilation from the Earth would cause the two masses to increase the number of gravitons they send toward the Earth, and thus decreasing the number of gravitons they send sideways, towards each other, and away from the Earth.
It sounds like the Canvendish experiment, and it should give a measure for G that it slightly less than the CODATA value: 6.674 08 x 10^{-11}. The stronger the gravitational time dilation, the more the gravitons are sent in a unidirectional fashion, toward the gravitational source.
Maybe, if pigs fly, and then only on Tuesdays.
Comment #71 February 5th, 2019 at 1:50 pm
Lou Scheffer #64
“You can’t count the whole Web as a benefit of LHC.” . Sure ,something similar would have appeared sometime , that is why it needs an economist to estimate all the probabilities, as in the link I gave about the cost/benefit of the LHC where the authors did not want to go into the part of technological progress.
Two years is unrealistic, there was no globalization then (1989), the cold war was barely ending, and communication needs for commerce and industry were covered with faxes and telephones for the companies. It was the universities and the research needs that were fulfilled by the web, and then the rest caught on.
But if one disputes the cost of new experiments, one should have a full cost/benefit study for society, not decide on esoteric minutiae of astrophysics instrumentation or what ever just on some theoretical models of whether a spectacular discovery would be made.
Please also note the quote attributed to Lord Kelvin ( and/or others)
““There is nothing new to be discovered in physics now. All that remains is more and more precise measurement.”
When one contemplates what came after these words, special and general relativity as far as theory goes, and quantum mechanics imposed by experiments, even before accelerator physics, it would be called a hubris.
The theories developed up to now for particle physics are at the level of the proposal of special and general relativity, at the beginning of the twentieth century, a model predicting new behaviors. It took 70 years for the standard model to be established and a great number of accelerator experiments by physicists fascinated by research in new energy frontiers. The present generation of particle physicists have the various phenomenological models lighting the way, but who knows what surprises nature has for us?
In my opinion it is hubris to say “we have reached a limit in understanding nature at the basic level” and try to defend it with money spent, when the gross world product is in the trillions and the FCC is asking for a few billions, which will eventually be returned to society even without new technology, in analogy with the cost/benefit for the LHC. And I am sure there will be new technology, because basic research attracts the best people ,and the enormous needs of the huge experiments will stimulate them to new heights (keeping my fingers crossed).
Comment #72 February 5th, 2019 at 1:51 pm
Hi Scott,
I asked this on TRF:
Is there such a thing as a gravitational quantum Doppler effect? I mean, the wavelength doesn’t change, only the probability of finding a monochromatic graviton changes?
Comment #73 February 5th, 2019 at 2:47 pm
Atreat #69
I just read your last response , and my impression is that you do not know what particle research is about.
It is established that the higher the energy of the projectiles in colliders, the smaller the dimensions that can be measured , the famous Heisenberg uncertainty principle at work. Thus particle research is about going into smaller and smaller distances with higher and higher energies . Each new collider opens a frontier into studying the microscopic structure of nature.
” First of all, “new physics” is ambiguous here. ”
It has to be ambiguous. If we really knew what we would find , why experiment? Does an engineer have to experiment to build a train line from one city to the other? He just has to design and calculate.
In physics research, and particularly particle research this does not hold. The models are maps which fit data and predict behaviors successfully for the present energies reached. Their predictions are guidelines for the new frontier desired with the FCC , but they are not written in stone as law. I am sure all researches will be delighted if something new comes up, and will be very happy even if signs of string theories extra dimensions can be measured, but even if the result is that there is just verification of the standard model to the limits of the FCC energies, this is a positive experimental measurement, weeding out various possibilities in models.
We would then desire even higher energies. I would hope though by the time the FCC would be history, new methods of acceleration not needing such huge tunnels will have been found. (Actually, in my opinion,there should be some money spent by the world community in parallel to the construction of an FCC in that direction).
Studying the behavior of matter with higher and higher energies should be separated from the success of prediction of models. When I started with neutrino physics in bubble chambers the model for the scattering depended on the parton model of Feynman and nobody expected to see jets. But jets did emerge at the next collider LEP experiments. It is possible that nature has surprises for us that if somebody told us now, would sound like science fiction.
Certainly a cost/benefit analysis should be done, and from the link I have given in my first entry, the LHC breaks even. It has not given anything unexpected, and has not revealed the spectra expected from the various models, but that is what research means. Studying the unknown including deserts. ( although there might still be surprises as all the data have not been analyzed yet and new energies are coming up).
“that there is a lack of clarity ”
The lack of clarity is on the part of those who confuse budgets, with basic research models.The world community can afford research projects and researchers should compete for the funds, but the argument for higher energy colliders should not just be validation of current models ( which will be validated even if nothing new is found) but the chance of a spectacular discovery as the new frontier opens up. “Here there be tigers” is what current theories tell us, but maybe we find elephants :).
Comment #74 February 5th, 2019 at 3:22 pm
YesIHaveAName #52
What you will be telling a generation of physicists and engineers is that a career in high energy physics is a waste of time. Then you will get stagnation, and with no new generation to take over you may as well close it all down. We are where we are due to a lot of historical contingency. Not all of it good, WWII, the Cold War, etc. You don’t just pull complex technical infrastructure out of your arse whenever you feel like it. Whats worse, is that we are heading into a world defined by Global Warming, mass migration, nuclear proliferation; while our governments are becoming more insular, less intellectual, and downright anti-science. Places like CERN will be very important over the next several decades as centres of international cooperation, high quality science education, and a constant reminder of the value of knowledge. Many of CERN’s scientists became administrators, civil servants and played an important part in shaping European science policy. All this is not something to be taken for granted.
I also don’t understand your remark about the Space Program. What progress? Manned space exploration is dead. The space station is just a tin can kept afloat by nostalgia. Every few years a new observatory or probe does go up, but they are few and far between. We could have done a lot better. Unless you meant the tiresome nerdfest of billionaires pretending they can fly to mars and other nonsense. But I consider you too intelligent to fall for such bullshit.
Comment #75 February 5th, 2019 at 3:33 pm
I suppose I shouldn’t be suprised given the nature of this blog that people here care more about computers than lasers, collimators, magnets, superconductors, and so on. So let me just add that in addition to our glorious WWW, other tech to come out of CERN (and other particle physics facilitites) include Grid Computing – a forerunner fo today’s ubiquitus Cloud Computing, and of course where would Big Data be without the Petabytes of data that needed to be processed. Take a look at some of the open source frameworks employed for these tasks, and where they came from, and who their main contributors were.
Comment #76 February 5th, 2019 at 4:11 pm
Can we distinguish between rationales for a new collider, published by CERN, and those put forth by others?
On the former: electroweak, Higgs, etc – how prominent are these? How about an economic case, for “spin-offs”? Retaining skills, jobs, and knowledge? Anything about serendipity? Why this $20bn is better spent on a new collider, rather than 20 $1bn projects which also produce spin-offs, retain jobs/knowledge/etc (there are surely lots of these)?
On the latter: several people, both here and in other blogs, have at least touched on most of these (though there seems to be little on the last point, and almost no one has presented some even modest $$ estimates). Surely it’s these sorts of details we should be demanding?
Somewhat unrelated: I have been dismayed to read some of the comments from self-described HEP physicists (not here I should stress) – ad hom attacks, “rebuttals” that do not address Sabine’s points, subjective and almost fact-free claims, and so on. The sort of thing I see from many a crackpot; where is their scientific integrity?
Comment #77 February 5th, 2019 at 4:35 pm
Anna V, #73
You start out with saying I don’t understand particle research and then go on for a few paragraphs adding nothing new at all. I know you would like to explore higher energies. I know you hope this will reveal new physics or information not yet gleaned from current experiment. I know that there is no guarantee with any theoretical prediction and that is why we must actually do the experiment to find out if nature agrees with our ideas of how she aught be.
This does not address at all the qualms I have echoing Sabine. It is one thing *not to have a guarantee* that we will see something new and quite another to have *no sound motivation for believing we will see anything at all* for our $20 billion. That is what Sabine is charging you all with. The fact that no one will take up her challenge other than to launch personal attacks or wax poetic about the general benefits of basic research is jaw dropping and does not reflect well on your profession.
Comment #78 February 5th, 2019 at 4:47 pm
Atreat #77: The reason you’re not getting a clear answer to your questions is not because people are intellectually dishonest but because there isn’t an agreed-upon answer. There are scenarios that some theorists strongly advocate, for independent reasons, where you absolutely would see new stuff at the 100TeV scale (but not the LHC scale), like superparticles or axions or whatever, where the new stuff would have to exist. And there are other scenarios where there’d be nothing new all the way up to the GUT scale or the Planck scale. And there’s no agreed-upon way to decide the relative plausibility of those scenarios.
If only, you might muse to yourself, there were some other means to settle such a dispute! 😉
Incidentally, from now on I’m instituting a zero-tolerance policy for personal attacks, from all sides. I’ve already banned “Dr. Sarah Goldstein” (presumably a pseudonym), for a comment (which I left in my moderation queue) that was dripping with snide/trollish attacks and that contributed nothing else whatsoever.
Comment #79 February 5th, 2019 at 5:17 pm
Scott #78,
“There are scenarios that some theorists strongly advocate, for independent reasons…” <-
Yes, and my understanding is these are (mostly) based on naturalness or aesthetic arguments and is precisely the point of Sabine's critique. If you want to do a collider for $20 billion with no rational expectation that we'll see any BSM physics then this is absolutely fine. I'd like to see people argue for that and would probably be sympathetic!
If, on the other hand, you think that there is a reasonable rationale for *expecting* to see BSM physics at higher energies after the LHC, then I'd like to see those people rebut Sabine without resorting to personal attacks and explain why in spite of all the failure that we should still resort to naturalness or aesthetics to predict that FCC or some larger collider will see BSM.
What I've seen is radio silence from those people who would predict BSM for the next collider and yet not admitting that this is what they are doing. Sabine is leveling some pretty serious arguments and yet those responding don't seem willing to wrestle with the meat of her critique.
The LHC was a success because if nothing else it confirmed the last accurate prediction of the standard model. However, there were a heck of a lot of *other* predictions that did not pass muster by way of nature. Sabine is saying those predictions were flawed from the get and warning against further predictions made on the same flawed grounds. If she is right, I'd like to see some prominent particle physicists responsible for those failed predictions say so and acknowledge as such. If she is wrong, I'd like to see them rebut her with ideas instead of nastiness.
Comment #80 February 5th, 2019 at 5:20 pm
Scott: the key part for me is “haven’t adequately reckoned with the failures” (or however you phrased it).
I’m just coming off another deep dive into the history of photosynthesis studies, and it seems to me that this is the usual way of science: crash through blindly, grabbing at ideas and people and money close to hand, frequently without understanding either the ideas or the other people’s disciplines well, often doing science of convenience, until enough pieces exist and cohere that ideas coalesce and don’t go flying apart very easily. And it’s not a great mystery why: there’s little incentive to slow the hell down, really comprehensively study and argue about what’s already been found, shake the data and see what it’s worth, and come up with a range of serious plans, ranked, before setting out again.
I think ALL the sciences would likely benefit greatly from an enforced 3-5 years’ worth of “stop and study the literature and think hard about where we are, what we know. Not just your literature. Adjacent literature. Historical literature. Literature that you don’t know yet is adjacent. You must go to meetings out-of-discipline, you must hear what else is known elsewhere. You should also invite outsiders, nonscientists, who will ask the kinds of questions you no longer think about, but should. In the last 18 months of this, or whatever, you’ll begin the report-writing and the recommendation-making. And anyone who starts to write selfish reviews gets kicked off the planet: you all have salaries (and we’ll sustain the ones on soft money, but not the labs), you’re FINE. Just stop for a little bit and assess.”
Immediately, of course, a massive outcry would go up about promotions and prizes and career stages and blah blah blah, for which I really have no sympathy, and the answer to that is: you want money from who, again? You want how much? Your salary is what now? Yes, well, you’ll be all right for a while.
Comment #81 February 5th, 2019 at 5:45 pm
Here is how I would argue against building a new accelerator:
QFT, General Relativity, and Statistical Mechanics each give us hints about how a unified theory is supposed to look like. People don’t really expect that these theories will change due to new empirical evidence. Details about the Standard Model might change, but the core algebraic structure would remain the same.
This means that even discovering something in that new accelerator would only delay the inevitable: that we have to go into a very deep introspection with only theoretical first principles in hand, and deduce a unified theory only from these. I claim that every clue is there in our hands already, just like how Lorentz had all the clues to deduce GR.
The fact that we had almost 50 years and failed shows that it’s hard, obviously. But machines might help. I expect we will be aided by intelligent machines that are capable of independently deducing GR from scientific evidence available in 1862. I bet those machines are cheaper than $20B, you could run DeepMind for 50 years with that money.
Comment #82 February 5th, 2019 at 6:46 pm
Atreat #79: People’s opinions differ here—there’s no individual who can “answer on behalf of particle physics” (leaving aside that if there were, it obviously wouldn’t be an outsider like me). Personally, though, if a next-generation collider discovered new particles, I’d say in retrospect that it was clearly worthwhile to build. If it didn’t—if it revealed a desert up to 100 TeV—I’d say in retrospect that it was kind of a wash whether it was worthwhile to build or not. Therefore, averaging over the two possibilities—neither of which dominates the other in likelihood for me—I conclude that it’s worthwhile to build. But you see how the calculation could shift to “it’s a wash” or “don’t build it” for the next collider after that, if nothing but a vast desert were found.
Comment #83 February 5th, 2019 at 6:49 pm
> none of the SSC budget, as in 0% of it, ever did end up redirected to those other subfields.
How sure of this are you, and why?
Comment #84 February 5th, 2019 at 7:44 pm
Scott #68: “I think there’s a strong case to be made that, had Berners-Lee not invented the web, whatever arose instead of it would probably have been more proprietary, centralized, and worse.”
This is a tricky case to make, as shown by this classic argument from biology. Suppose, for example, that the rate of biological mutations had suddenly doubled about 20 million years ago. How does this affect when humans arise? You can argue with a straight face any of these three scenarios: (a) Humans arise earlier, since evolution runs at double speed. (b) Humans arise later, since the increased mutation rates enable the existing forms to keep up better, or ( c) There is no effect, since mutation rates are themselves selected for, so the main effect would be to evolve better DNA repair mechanisms to get the rate back to where it was.
As critics have pointed out, a theory is hard to falsify if, when following a factor of 2 change in your main variable, you can’t even predict the sign of the result. I think the same is true here – if CERN did not invent the web, it might now be better, worse, or the same.
Comment #85 February 5th, 2019 at 7:46 pm
I’m not sure that it’s a good idea to make things so personal. But this never works. No one ever gets credit for negative predictions. At most it reinforces their reputation as “not a team player,” even more than if the prediction had been false.
In particular, there was a huge chorus of people predicting new physics at the LHC. Why have you not penalized the reputations of these people? Why are you still crediting them when they predict that this new collider will have new physics? If you make such appeals to authority, how else can I respond but with ad hominem, accusing them of intellectual dishonesty, or, to be more polite, déformation professionnelle.
That is gerrymandering. The LHC produced no new physics. It produced just a measurement of the Higgs mass. If it had failed to find the Higgs, that would have been disturbing, bordering on new physics (although there was a long history of falsified predictions of the energy needed to find the Higgs, so maybe I shouldn’t trust the physicists who claimed that it would have been disturbing). The LHC has already found the energy desert.
Comment #86 February 5th, 2019 at 8:07 pm
Amy #80 said ” I think ALL the sciences would likely benefit greatly from an enforced 3-5 years’ worth of “stop and study the literature and think hard about where we are” […] In the last 18 months of this, or whatever, you’ll begin the report-writing and the recommendation-making.”
The astronomy and space science fields do almost exactly this. They are called ‘decadal surveys’ and happen every 10 years as the name implies. They take a pretty serious look at what is known, and try to prioritize what experiments could be done over the next 10 years. They are run by a more-or-less neutral body (the National Academy of Science) and seek input from all the sub-fields, grind it all together, and then write a report with recommendations. The results are not without controversy, but funding agencies take them seriously.
They have been quite successful at deciding which big experiments to fund, and there are are many folks (myself included) who think that many more fields could benefit from this level of analysis.
See this task specification (or just do a web search for ‘decadal survey’) http://sites.nationalacademies.org/cs/groups/ssbsite/documents/webpage/ssb_190177.pdf for an example of the survey mission.
Comment #87 February 5th, 2019 at 8:43 pm
Douglas #85: Hey, I don’t actually have a dog in the fight about BSM physics; I’m just an interested spectator. 🙂 Anyone who confidently predicted superparticles, etc. at the LHC does now have a lot of reflecting to do, before we take seriously any of their further predictions—Sabine is right about that! But the truth is, almost none of the particle physicists who I talk to did predict that. They simply adopted the position that they didn’t know and that we should find out.
The situation might be a bit analogous to the one in QC, where a few loud people confidently predict (e.g.) scalable devices in 5 years, or exponential quantum speedups for optimization, or whatever, and those predictions get amplified because they’re what outsiders want to hear, and then later the QC skeptics try to throw those predictions in my face and make me answer for them, as if I shared in the responsibility for them—even though I was actually throwing as much cold water on wild claims as I had time and energy for, and a google search proves it! 🙂
Comment #88 February 5th, 2019 at 9:01 pm
Lou #86: that’s immensely helpful. Thank you very much. I had no idea.
Comment #89 February 5th, 2019 at 9:35 pm
amy #88: Yes, I was going to say what Lou said better, that there’s a huge amount of formalized discussion and reflection that already goes into planning experiments of this size. Those involved in it tend to see blogs, editorials, etc. as just a way for the losing side of that process, the side that couldn’t convince fellow experts, to try to short-circuit it by appealing to the populist impulses of non-experts. In their minds—and I’m not saying I share this view!—Sabine is just like the climate deniers, who go to the public because they know they can’t sway the IPCC.
The other issue, though, and one that’s extremely specific to particle physics, is the decades that it now takes to plan and build these colliders. If CERN or whoever else wants a new circular collider by the late 2040s (!!), it should start right now.
Comment #90 February 5th, 2019 at 11:47 pm
1. Scott, you keep using the phrase “independently motivated scenarios.” What does this mean? Independent of what? Independent of the existence of the LHC? I don’t believe it. It’s motivated reasoning. Scenarios independent of each other? That’s moot, since they’re dependent on the LHC.
2. You don’t name your sources, except for one talk, by someone who did confidently predict supersymmetry at LHC, enough to bet on it. Should you take that into account when assessing his current predictions, his claims about current scenarios, and his description of the past?
We should applaud public bets. They forced precision on his predictions and they forced him to confront his failure, rather than just quietly erasing history as most of his peers did.
3. I’d rather have polls than relying on celebrities and bets. This claims that those who attended the bet resolution ceremony were polled and a majority predicted new physics at LHC in the next 20 years. Well, if the LHC is still going strong, what’s the hurry on a new collider? 😉 [I don’t know what they mean by “LHC”; my guess is some upgrades, but not FCC.]
I’m really confused by this poll. I thought that most people had given up on new physics, that if it was going to be seen at LHC, it would have been seen quickly. In the sequel I will treat it as a pre-LHC poll. I’m not sure what conclusion I should draw from the real timing.
4. No, of course we shouldn’t “punish the errant theorists.” We shouldn’t allow a few loud voices to do anything. I could be wrong, but I don’t think that we should personalize it or talk in terms of punishment. But we should try to force some consistency on our collective beliefs and decision procedures. If people really expected that LHC was not powerful enough to get new physics, then just the search for the Higgs could have justified it; and new physics could justify the next thing. But is that what they expected? If, as the poll suggests, people expected new physics at LHC, how much are they allowed to expect new physics now? If they expected new physics then, we have had the failure, the one null result in the energy desert that you said justifies stopping. (It would be better to make this more precise in the form of a prior distribution of the energy level of new physics, as of 1995, and see what updating really looks like.)
5. A lot of this feels like an argument about whether it is OK to lie to politicians (“same arguments as those used to promote the L.H.C. in the ’90s”). Insiders argue that they can keep track of the truth despite the lies. As an outsider, I’m offended that they pollute my sources of information. Also, I’m skeptical that they really do keep track of the lies.
—————
The issue of very large parameter spaces reminds me of the problem of heliocentrism. Aristarchus (apparently) argued that since the sun was 10x the linear size of the earth that the earth must revolve around the sun. That implied that the fixed stars must be very far away, but he bit that bullet. Around 1635, Wendelin measured that the sun was actually 100x the linear size of the earth, thus the fixed stars would be another 10x as far away. Just based on this measurement, should one update towards or away from heliocentrism?
[1635 is earlier than I remembered. It should have had some role in the modern fight over heliocentrism, but I don’t think that it did. What would history have been like if Copernicus or Brahe had tried to redo this measurement?]
Comment #91 February 6th, 2019 at 12:35 am
Atreat #77
In my opinion, you are confusing apples with oranges In the decision making policy.
apples: the scientific defense for going to higher energy interactions
oranges :the money needed from society.
Presumably society has a budget to be distributed for research, which by definition of the term is a gamble. ( it would be good to see the statistics of how successful research is)
Experiments apply for this financing, and should be judged by a) cost effectiveness, and b)peer reviewed opinions.
It is not a peer review to use a blanket argument “nothing will be found because that is what I expect, as I think anything that can be found has been already found”. It is based on Lord Kelvin’s logic, which has been falsified over and over again, certainly by the history of going to higher and higher energies in particle physics. It is also not a cost effectiveness review.
Comment #92 February 6th, 2019 at 1:05 am
Atreat 77
Actually the statement by Lord Kelvin would be a peer review, by one peer. Fortunately his opinion was not asked for the funding of future experiments.
I have not yet heard that the FCC has applied for funding, for unasked peer reviews to be vociferously offered. I am sure the reviewers are chosen carefully, and the reviews will not be on the internet.
Comment #93 February 6th, 2019 at 1:46 am
Douglas Knight #85: Regarding “penalizing the reputation”, it will not work. I observed there are people who are always on the smart side. Whatever happens. What I don’t know is whether it’s a skill that can be taught, or an ability that one has to be born with.
Comment #94 February 6th, 2019 at 1:58 am
Atreat #79
>Sabine is saying those predictions were flawed from the get and warning against further predictions made on the same flawed grounds.
Theoretical models can be flawed if their mathematics is wrong . The premises are a matter of choice, and data trumps theories, so if the premises are wrong the theory will fall by the wayside.
Is Sabine the Pope? There are no Popes in research. By construction it is a gamble whether a prediction will manifest or not in a research endeavor in any discipline.
>If she is right, I’d like to see some prominent particle physicists responsible for those failed predictions say so and acknowledge as such
All theorists can form theories that predict the future, which may not manifest. Feynman for a long time fought the quark model and stuck to his partons. Should he have apologised? what he did he identified the partons with the quarks and went on from there.
If the predictions could not fail, they would not be predictions, they would be engineering plans. Of course there is no need for theorists to apologize for a model failure. They just have to adjust their parameters that correspond to the measured experiments.
The basic physics question to be answered is : should we go to the highest energy possible in our search of exploring nature? And the answer is yes, because it payed off in the history of physics.
Then one should ask : is it cost effective for society? And the answer is yes, as seen in this link for LHC and I am sure it will be for the FCC
https://indico.cern.ch/event/398256/attachments/798707/1094710/CERN_slides_v_4.pdf
Comment #95 February 6th, 2019 at 2:01 am
[…] weighing in with lofty rhetoric , kept in mind quantum computing physicist Scott Aaronson using a more competent defense , and Hossenfelder not surprisingly revealing aggravation at the entire organisation. This plainly […]
Comment #96 February 6th, 2019 at 3:04 am
Question:
I am not a physicist. From what I understood there is supersymmetry, string theory, particle physics from the one side. What is the other side of the state of affairs in theoretical physics today.
What are their proposed experiments and why they are not heard in the media? Thanks.
Comment #97 February 6th, 2019 at 3:07 am
Not a physicist #96: Your question doesn’t make much sense. Why do you assume that there are exactly two “sides”?
Comment #98 February 6th, 2019 at 3:37 am
@Scott
Yes correct.
I mean, from what I read, the mainstream research in Theoretical Physics today is on supersymmetry etc. or at least this is where most of the research grants are going.
My question is which other theories, that could lead to some large scale experiments, exist in the field?
The general audience information on the matter is scattered and vague. Thanks.
Comment #99 February 6th, 2019 at 3:54 am
I believe that big new experiments are worthwhile, not as an efficient investment, but as a desperate, Hail-Mary grasp at a fleeting hope. Elementary theoretical physics is in deep, deep trouble. All of this wandering around in speculative, not-even-wrong mathematical Never-Never-Lands; the stuff Sabine and Peter Woit love to hate – it’s all the result of the basic ground reality that for thirty years now, we haven’t had any unexplained phenomena with enough detail to build a model around. Science needs something wrong, something to work to make sense of. If we don’t get that, HEP will keep on descending further and further into its own imagination, and all connection to “explaining Nature” will be lost.
So our best hope is that, if we go ahead and explore where no-one yet has, then maybe, just maybe, Nature will sneak up behind us and bash us over the head with detailed, quantitative observations that make absolutely no sense to us. It’s not likely, but the alternative – the status quo – is too dreadful to accept.
Comment #100 February 6th, 2019 at 4:22 am
Scott #82:
Suppose it did reveal a desert. Also suppose it gave us incite to develop an accurate model of proton spin. Also suppose it put enough constraints on the properties of quark-gluon plasmas that astrophysicists could use to make predictions about the early universe. Also suppose that it played a part in the development of a new generation of superconductors and collimators.
Would you still call it a wash?
Comment #101 February 6th, 2019 at 8:04 am
Bunsen Burner #100: If the particle beam also toasted bread and cooked vegetables, then no. 🙂
Comment #102 February 6th, 2019 at 8:27 am
NAP #98: That was precisely what I was thinking I should read Sabine’s book to learn her answers to. The best-known alternative to string theory is loop quantum gravity, along with related ideas like spin foams. And I know that the proponents of those ideas are always wanting to get better observations of ultra high energy cosmic rays—for example, to see whether there’s some signature of the discreteness of spacetime, or of a modification to special relativity. Needless to say, nothing of that kind has been established, although I believe it’s still unexplained where the very highest-energy cosmic rays come from, and how they’re able to reach the earth in the numbers they do.
Besides that, the other big hope you always hear about is that observations of the cosmic background radiation will tell us more about what was happening in the inflationary epoch, and that that in turn will advance high-energy physics—in effect, exploiting the Big Bang as the universe’s best particle accelerator. You might have heard about the great excitement a few years ago when people thought they had detected “B-modes” from inflation, which was unfortunately short-lived (it turned out to be galactic dust).
Whatever the experiment, though, in some sense it must involve either extremely high energies or new phenomena of gravity/cosmology (or both)—since as long as we’re talking about low energies, in situations where we already know the behavior of gravity, the existing Standard Model has got you covered.
Comment #103 February 6th, 2019 at 11:15 am
Dear Scott,
Why don’t *both* you and Sabine get *this* part right, viz., that it’s *entirely* about keeping the ongoing jobs intact—the ones which one “manfully” got years ago, even if it necessitated in the process deriding many other “manful” intellects all along the way.
OK. Let’s leave this part aside, but still, honest:
How many smart people would be discussing these (or such) things if it were not for the fact that almost every “rational” source of funding these days is public, not private—no matter what influence the *supposed* “private” “sector” exercises into the allocation of every possible public funding or the decision (and vice versa)?
[May God *actually* damn this mixed-economy business!]
Since I don’t want to devote a post exactly at this point of time about it at my own blog, let me mention just one more thing:
If I personally were to have had, say, a US $200 B at my disposal, or a US $ 2 B, then, *I* would invest a very significant part of it not into artificial intelligence (the area which currently promises to be my best hopes of obtaining any mode of survival for myself anyway), but into the area of the artificial photo-synthesis. Too few people (except for, notably, those at the God-forsaken Berkeley or so) do it very seriously. There should be many more such places, if you ask me. But again, that’s an aside. [Personally, I care for my own survival far more than whatever else that I end up writing.]
Best regards and wishes, not just to you and all, but also to Sabine, whose fight-it-back spirit I have come very much to appreciate—such a spirit has been overdue, if you ask me…
…Anyway, bye, really, for now…
–Ajit
Comment #104 February 6th, 2019 at 11:24 am
I would recommend reading Sabine’s book. She presents a clear argument and gets some surprisingly funny interviews with interesting people.
I also don’t see many people engaging with the heart of her argument, that arguments motivated by “naturalness” are unscientific. You can’t talk about the probability of a value being one thing vs. another without first choosing a probability distribution and you can’t derive the distribution from first principles.
Why is this larger collider the best choice? Maybe it really needs to be twice as big to find anything interesting. There is the economic/technology investment argument, but with that. criteria maybe a space based collider would be even better.
Comment #105 February 6th, 2019 at 1:06 pm
Michael #104: I’d say there’s a form of “naturalness” that’s almost tautologically true. Namely, when a bunch of huge positive and negative terms almost perfectly cancel each other out, there must be some explanation for it. The explanation might not be supersymmetry, or any other symmetry, or even the anthropic principle. It might be something so strange that no one has thought of it yet. But at any rate there’s some explanation. And probing nature at higher energies is just the most obvious way to look for clues about that or nearly anything else that isn’t explained by the Standard Model.
Personally, I feel zero attachment to supersymmetry or any other specific proposal for BSM physics, to whatever extent I even understand them. And I think it’s a mistake to make the case for a new collider on the basis of any specific proposal, and you’ll notice that I didn’t. The motivation is to see what’s there.
Comment #106 February 6th, 2019 at 1:31 pm
Scott #105,
I agree that there must be *some* explanation for near-perfect balancing of large numbers, but you have a hidden assumption that I am not sure is warranted: that the explanation must necessarily be meaningful or revelatory rather than mundane, trivial or an artifact/bug of a particular model that is nevertheless very useful.
Comment #107 February 6th, 2019 at 2:08 pm
Scott#105, I’m surprised by this comment:”I’d say there’s a form of “naturalness” that’s almost tautologically true. Namely, when a bunch of huge positive and negative terms almost perfectly cancel each other out, there must be some explanation for it.” If the result is to be a probability, then you know in advance it must be in [0,1], but the calculation of it certainly could involve a huge amount of cancellation. Isn’t this what a quantum computer could be seen as successfully doing – summing a huge number of numbers and getting a small result, i.e. |sum a_n|<<<<sum |a_n|. Perhaps the existence of such an "explanation" of this would contradict your beliefs about quantum complexity.
Comment #108 February 6th, 2019 at 2:36 pm
abc123 #107: Quantum computing is actually an example par excellence where what I said is true. Given some quantum circuit on n qubits, you can decompose the amplitude of any output string as a sum of exponentially many contributions, one from each possible “path” leading to that string. The sum of the absolute values of the contributions could be huge. And yet, when you sum the contributions themselves, you find that probability is always conserved. That is, for all but at most a few of the output strings, almost all the contributions to their amplitudes interfere destructively and cancel each other out, so that the 2-norm of the vector of amplitudes is still at most 1, rather than something exponentially large. Why? What’s the explanation for this miracle of cancellation?
Unitarity. In this case, the unitary of QM is the full and complete explanation.
Comment #109 February 6th, 2019 at 2:45 pm
Anyone knows whether some of the tech used in the LHC has been ported over something more practical like fusion reactors (Tokamak and such)?
Comment #110 February 6th, 2019 at 2:49 pm
In terms of alternate hugely expensive experiments that could produce earth-shattering (not literally) results…how about Roger Penrose’s proposed FELIX experiment to confirm “orchestrated reduction” in quantum physics? I gather about .01 percent of physicists believe it would yield the result Penrose expects, but it sounds like a neat project.
Comment #111 February 6th, 2019 at 2:55 pm
Bob #110: Like my UT colleague Steven Weinberg, I’m a big fan of doing better precision tests of quantum mechanics—not just to put constraints on Penrose-like models, but in every other direction as well! Indeed, one motivation for quantum computation is that it will test QM in a regime of “fault-tolerant superpositions” where it’s never been tested before.
Having said that, if one’s objection to a proposed experiment is “we have no reason to believe this will return a non-null result,” then I think that objection applies with approximately a thousand times more force to a test of Penrose’s Orch-OR model, than it does to a higher-energy collider! 😀
Comment #112 February 6th, 2019 at 3:04 pm
We’ve never conducted experiments where thousands or millions of particles/qubits interfere with each other.
I still wonder if we won’t hit some kind of non linearity at some point, similar to how photons can start interacting with each other in vacuum (breaking the supposed linearity of the EM fields).
Maybe we’ll reach some limit on the wave function complexity way before we reach some maximum information density.
Comment #113 February 6th, 2019 at 5:41 pm
@fred #112
“We’ve never conducted experiments where thousands or millions of particles/qubits interfere with each other.”
Doesn’t practically any experiment on a macroscopic system involve that ?
I’m way out of my depth here because my knowledge of quantum computing is very limited but I’m a bit confused when people say that quantum computing is testing some ability of quantum systems to support cancellation of enormous numbers of complex amplitudes.
One thing I know about quantum mechanics is that it has a classical limit, which is absolutely essential because otherwise the classical world we perceive would not exist. It’s also my understanding that this classical limit results from the cancellation of many amplitudes for non-classical behavior.
If this is true than why should we consider the possbility of such a process in a quantum computer to be in doubt ?
Comment #114 February 6th, 2019 at 7:12 pm
Gerard #113: No, if it’s the classical limit, then basically by definition of the classical limit, the various branches are not interfering with one another (i.e., contributing to the same amplitudes), but are just evolving independently. Whereas in any interesting quantum computation, the branches would have to interfere.
Comment #115 February 6th, 2019 at 7:30 pm
@Scott #114
OK, it’s possible I completely misunderstood or am mis-remembering my quantum mechanics from 30 years ago but how does what you say accord with this statement from the wikipedia article on the classical limit ?
“In a crucial paper (1933), Dirac[7] explained how classical mechanics is an emergent phenomenon of quantum mechanics: destructive interference among paths with non-extremal macroscopic actions S » ħ obliterate amplitude contributions in the path integral he introduced, leaving the extremal action Sclass, thus the classical action path as the dominant contribution, an observation further elaborated by Feynman in his 1942 PhD dissertation.[”
Link: https://en.wikipedia.org/wiki/Classical_limit
Comment #116 February 6th, 2019 at 8:10 pm
Scott #108: Hmmm I think I garbled my point since it is really two somewhat incompatible points. On the one hand since the quantum circuit example gives an example of massive cancellation that is explicable (unitarity), then maybe other cases of massive cancellation shouldn’t be seen as such a big deal – nature ostensibly just likes to compute huge sums with massive cancellation. On the other, completely different, hand, maybe I want an even better explanation to understand what’s really going on when quantum circuit achieves this massive cancellation, and the kind of explanation I actually want would take the form of a polynomial size classical circuit that can do the same computation, and it’s this kind of “explanation” that would contradict complexity conjectures. Anyway, maybe I got off topic.
My on-topic thought: The really strong point made by Sabine and others, is that some parts of theoretical HEP have gone totally off the rails over a few decades. These theorists created wild theories that have failed to match reality. And many say that it’s not just a case of perfectly decent theories that just happened to not match later experiments, but rather, that they were intrinsically flawed ideas to start with, and credence should not be lent to such ideas when choosing future experimental directions. A question (separate to the collider building merits) is how/why did this happen. While there are some pretty flaky departments on campuses, it shouldn’t be happening in the hardest of hard sciences. It’s quite shocking, and I don’t think the lack of experimental data at times is really an excuse.
Comment #117 February 6th, 2019 at 8:45 pm
Gerard #115: It’s certainly true that quantum mechanics is the thing that gives rise to the classical limit in the first place. In particular, the fundamental explanation for the principle of stationary action, which is so important to classical physics, is indeed that all the paths whose action isn’t stationary have wildly oscillating amplitudes that interfere destructively and cancel each other out (that was Dirac and Feynman’s big insight). At the end of the day, though, it all adds up to a branching tree of classical-looking paths, which diverge whenever there’s a quantum decoherence event and which never again recombine. If you wanted to simulate such a process on a classical computer, you could easily do so by just following a single path, and using a random number generator whenever a branching event happened, in order to choose which way to go. In an interesting quantum computation, by contrast, the “paths” would constantly recombine, thereby frustrating any attempt at a simulation along those lines. No, I don’t think that means QM is going to break down, but some of the quantum computing skeptics do think so, and they won’t be fully and completely refuted until we can actually build the scalable devices.
Comment #118 February 7th, 2019 at 12:04 am
Lou Scheffer #86
Amy #80
In HEP it is called “workshops”
https://conferences.fnal.gov/hadroncollider/announcement1.html
https://conferences.fnal.gov/hadroncollider/announcement1.html
What people do not realize is that building a collider takes almost as long as a cathedral and demands not simple laborers but high performance experts in various fields , as labor now is done by machines. It took more than twenty years to build the LHC which started functioning in 2008. And a lot of workshops before.
https://www.aps.org/publications/apsnews/200810/lhc.cfm
This is from 2008:
“Work on the LHC started in the early 1980s, and official planning began in 1984–five years before its predecessor in the tunnel, the Large Electron-Positron collider, had even started”
That is why this economic study can show a break even for LHC costs to society, there is a lot of give and take to society even before counting in the technological innovations introduced .
https://indico.cern.ch/event/398256/attachments/798707/1094710/CERN_slides_v_4.pdf
Comment #119 February 7th, 2019 at 1:33 am
abc123 #116
” These theorists created wild theories that have failed to match reality. And many say that it’s not just a case of perfectly decent theories that just happened to not match later experiments, but rather, that they were intrinsically flawed ideas to start with, and credence should not be lent to such ideas when choosing future experimental directions ”
Theories in HEP are mathematical models. The fact that the people who propose them are called particle theorists and not mathematicians is because their model has extra axioms/principles/laws that are imposed on the strict axiomatic solutions of their model, so as to fit present physics data and presumably be able to predict future behaviors for experimental setups.
If the prediction of the models fails, they fall by the wayside, and modifications have to be imposed on the premises , or be discarded completely. If they fit the present data, they are candidates for attempting to fit future higher energy data not yet attained.
What I am trying to say is that in theoretical HEP models it is the PREMISES , the extra axioms that are important. To decide that a model is flawed, needs the check of the data.
For example Feynman was a strong proposer of his parton model (no structures). Data in the end of 70’s refuted this by showing high p_transverse that indicated hard core scatterings consistent with the emerging quark model. Feynman then identified his partons with quarks. The model was flawed because of the PREMISE that all partons were equal in interacting with the leptons. Nobody came up saying the department that had Feynman was “flaky” when the original parton model was falsified.
The misunderstanding lies in assuming HEP theories are written in stone. They are mathematical gambles on what nature is about at the next level of energies that may be falsified due to an unexpected ball thrown by nature that needs NEW PREMISES for the mathematical modeling.
So theories are useful as a map with “here there be tigers” only for a set up of the instrumentation and the programs to study the data ( Monte Carlos), and I am sure that most experimental physicists are looking for the unexpected ball sent by nature, the way it sent us quarks instead of partons.
As I said above, the decision for a new collider based on physics models should go through a peer review, not a smearing campaign on the internet based on who knows what personal prejudices. A number of peers should judge the physics attainable at the FCC or any other collider. In parallel there should be a cost/benefit to society study as the one done already for the LHC, which I have linked in another posting above.
Theoretical models come and go if they are falsified.
Cost/benefit to society is what to look for when deciding about whether the money should be allocated. The LHC study shows that the probability that the LHC will break even by a return to society in training people and education, without taking into account the advance in distributed computing and data transfers and storage , is 95% . I.e. it will have cost the contributing countries tax payer 5% of the original cost (~5 billion) .
Comment #120 February 7th, 2019 at 1:45 am
Anna #119: If the LHC’s expected economic benefit to society is almost exactly the same as its cost (95% of it), isn’t that an unnatural coincidence demanding a new symmetry principle to explain it? 😉
Comment #121 February 7th, 2019 at 2:34 am
Btw, on the topic of Hossenfelder’s book, I don’t know that I can really recommend it if you already read her blog. I read the book and found it didn’t really go into substantially more detail. Basically the main selling point it actually does have over the blog is the interviews. But this seems to be mostly a matter of “social proof”, i.e. the significance is all in that it’s big-name physicists talking about these issues and at least partly agreeing with Sabine. It doesn’t actually go into more technical detail than you’ll find on the blog.
For instance, I recall Hossenfelder writing somewere on her blog (sorry, too lazy to find it right now) that while it initially seems difficult to invent new theories that extend the standard model and fit the existing data — so that each one is significant, each one’s falsification means something — once you really have a good understanding of QFT, it’s actually quite easy, which is why there’s such a barrage of them. Something she wrote in that post gave me the impression that something about how this is done would be explained in the book. This was not the case.
Similarly, going by memory I do not believe you will find in the book answers to such questions as “What experiments does Hossenfelder think should be done instead?” or even that much about “What other theories are out there?” (to list the two questions that were mentioned upthread). It’s not a bad book, mind you, it just doesn’t add that much on top of the blog posts. I ended up leaving it at my parents’ house, figuring maybe they’d get something out of it, since for them it’s an entirely unfamiliar topic. 😛
Comment #122 February 7th, 2019 at 2:36 am
Btw, probably the most interesting part of the book was the interview with Garrett Lisi, with his insistence on geometric naturalness.
Comment #123 February 7th, 2019 at 3:43 am
Scott #120
> isn’t that an unnatural coincidence demanding a new symmetry principle to explain it?
I am sure that if one made a cost/benefit analysis of the resources spent in building the cathedrals, the return in people finding work etc in the equivalents of that time would be again close to positive. The principle is sociological in the decisions taken by the rulers of the time, i.e. not within the realm of physics and mathematics, as also will happen with the FCC decision, by those who hold the purse strings. The SSC in Texas was not stopped because of physics predictions. A ruler has to gauge for a balance in input output resources, probably a lot of intuition enters in this, so it should not be surprising.
The reason I am taking part in these discussions is because I am upset that a smearing campaign by conservative minded people may give ammunition to politicians who hold the purse strings. That is why I am emphasizing the cost/benefit , that the eventual cost of an FCC or an ILC will be returned to society.
If the money factor is taken out, it is a matter of taste for politicians whether to spend it on FCC or building cities under water. Only the “crossing a new frontier” and “exploring” can be the dominant argument for ruling bodies, supported by the benefits up to now for new technologies .
Comment #124 February 7th, 2019 at 5:43 am
“I’d say there’s a form of “naturalness” that’s almost tautologically true. Namely, when a bunch of huge positive and negative terms almost perfectly cancel each other out, there must be some explanation for it. The explanation might not be supersymmetry, or any other symmetry, or even the anthropic principle. It might be something so strange that no one has thought of it yet. But at any rate there’s some explanation. And probing nature at higher energies is just the most obvious way to look for clues about that or nearly anything else that isn’t explained by the Standard Model.”
Thank you. Finally someone demonstrates, as briefly as possible, that SH’s main argument is completely nonsensical.
Comment #125 February 7th, 2019 at 5:45 am
Scott #120 continuing:
I just remembered a story about an old Sultan in the Ottoman empire, who, when leaving the empire to his son told him “construct, construct, construct” to keep the people happy, i.e. in jobs. In many civilizations this could be applied as a balanced cost/benefit rule.
The following should be a lesson for the detractors of the effort for the FCC , the monetary effect of cutting the SSC:
https://www.aps.org/publications/apsnews/201310/physicshistory.cfm
>The decision did not lead to increased funding for other areas of physics. In fact, the biggest beneficiary was the LHC, as the US particle physics community successfully lobbied for a greater role in the international collaboration. That investment paid off handsomely with the discovery of the Higgs boson.
Comment #126 February 7th, 2019 at 5:45 am
One more thing: as good scientists, we should be looking to settle this dispute by means of an experiment. SH keeps telling us that we are all failures and should try a new approach. This has in fact been tested experimentally: Erik Verlinde’s “entropic gravity”.
Case closed.
Comment #127 February 7th, 2019 at 11:11 am
Arguments against the planned SSC in the US from Phil Anderson in 1987: https://www.the-scientist.com/opinion-old/the-case-against-the-ssc-63734
Comment #128 February 7th, 2019 at 1:39 pm
I think it is quite reasonable to be concerned about the expensive of the project given its uncertain benefits, for three reasons.
First, while it might be true that the funds for such a unique “big, expensive, exciting” project will not be drawn directly from the pot of money funding common research projects, they might very well come from the potential funds available to finance other similar “big, expensive, exciting” projects! We’ve built a lot of colliders — maybe it’s time to push for an expensive blue-sky project in another area with higher potential benefits? And anyone thinking of doing this would probably enjoy greater success if we hadn’t just cut a $20B check for another venture.
Second, in the event of a major failure, such an expensive project would prompt a lot of bad press. This would likely make governments more hesitant to fund similar projects in the future. Thus the project might reduce future funds available for such projects even as it takes up current funds. (Arguably, the only reason new projects of this kind are so readily countenanced is due to the success of past ones — but that logic works in reverse as well.)
Third, while the funds may not be taken from science funding, they will be taken from somewhere. And while governments doubtless fund many less useful things, there’s no more reason to think that the money will be taken from the worst use of funds than from the best use. I’m all for new science, but if the likely benefits are not so great, and the funds may come from useful programs, then perhaps it is not worth it.
Comment #129 February 7th, 2019 at 11:16 pm
Do you think a super huge, beautiful, linear accelerator along the southern border would make us great again, again?
Comment #130 February 8th, 2019 at 2:23 am
I assume there are many physicists (plus Scott :-)) following this blog, let me also ask an offtopic question regarding quantum teleportation, which keeps confusing me.
Suppose Alice and Bob are in the same inertial frame K, and at time t (in K) Alice teleports a quantum state to Bob. What I always hear is that this means that at time t, Bob has then got one of four states, although he does not yet know exactly which one of the four.
Now, what if Alice and Bob are both moving along the x-axis of K, in the same direction, both with the same speed v? If Alice does her part of the protocol at time t (again, as seen in K), can we say that Bob will get one of the four states also at t? Or is there another formula in this case for Bob’s “delivery” time relative to K?
Because if in K, Bob is behind Alice (w.r.t. their common direction of movement in K), then his delivery time must be *before* t in K, due to special relativity. This sounds weird, as if the cause had happened after the effect.
Another confusing thing: what if Alice and Bob are *not* in the same inertial frame? Then the point in time Alice executes her part in her inertial frame does not correspond to any single point in time in Bob’s inertial frame. So what can we say about Bob’s delivery time of the quantum state (one of the four)?
Please correct me, I’d like to know the solution.
Comment #131 February 8th, 2019 at 4:02 am
jonathan #128:
No, you live in a world of fiat currencies. Governments use the same fiscal and monetary mechanisms to fund public works be they hospitals, stealth bombers or particle colliders. The pool of money you dream about doesn’t exists. Money is a social fiction that governments can make appear or disappear depending on macroeconomic need. This fantasy some people have the national budgets works like their wallets needs to die. Its a naive view contradicted by pretty basic macroeconomics and finance. Repeat after me until you get it: National finance is not househlod finance.
Comment #132 February 8th, 2019 at 4:17 am
jonathan #128:
Oh, and let me address the failure remark, which displays a grasp of scientific progress that is more reductive and one dimensional than even the economic argument. This is not some silly school exam with a facile pass/fail grade at the end. This is a complex social and cultural endeavour and needs to be evaluated as such. Anna V has provided numerous sophisticated example of how to do this, but they seem to have fallen on deaf ears. Let me just leave people with this thought. The next generation of lasers, superconductors, magnets, collimators and so on has to come from some where. Colliders provide new research opportunities in dozens of scientific fields. This allows us to improve our scientific instrumentation via a steady progress of incremental improvement. Once this process is shutdown the social case for starting it up again will a lot harder to make, and will be significantly more expensive and risky than the path we are on now.
Comment #133 February 8th, 2019 at 5:55 am
Bunsen Burner #131 and #132: This is a warning; any future comments with a similar tone will be left in moderation.
Comment #134 February 8th, 2019 at 9:42 am
Bunsen Burner #131 and #132: In spite of your tone two remarks warrant reply:
“No, you live in a world of fiat currencies…” and therefore budgets don’t matter and we live in a world of infinite resources?? Are you somehow extrapolating from the true fact that household budgets are different from national budgets the conclusion that there is no opportunity cost in developing a $20 billion new collider?? That because we live in a world of fiat currencies that a nation’s resources are somehow infinite?? Why not go for a $100 billion new collider then?? Why not go for $250 billion visit to the moon in next decade?? Why not go for even larger experiments and endeavors? Is there any limit??
“Anna V has provided numerous sophisticated example of how to do this…”
I found Anna’s comments as mostly lecturing us on common and trivial methodologies of science in a way that is completely orthogonal to Sabine’s argument(s) for whatever reason.
“The next generation of lasers, superconductors, magnets, collimators and so on has to come from some where.”
Sure, there are knock on effects of developing a next generation collider even if it discovers no BSM physics and maps out the Higgs. Again, no one is disputing that a next generation collider will have *some* positive effects. The question is whether that is worth $20 billion and the opportunity cost lost to other experiments. I’m sympathetic that we should do it. Sabine is not as sympathetic. People can disagree about this.
However, that is *not* the thrust of Sabine’s argument and again no one is addressing it. She says the hope of finding BSM should not be used to justify the next collider. Why? Because she says their exists no well motivated reason for thinking so. Some people **really don’t like** that she is saying this because they fear that it will lead the public to not support a new collider. They want to leave the question of BSM as hazy or ‘good people reasonably disagree’ even though I haven’t seen *any* prominent theoretical HEP physicist stand up and say she is wrong. They just hate that she is informing the public.
Scott says I’m wrong to think that there should be a single spokesperson for HEP that will challenge or rebut Sabine with good faith reasoning. But I don’t want a single spokesperson. I want *one* person of this large profession to step up. Just one. You don’t have to be a spokesperson just speak for yourself. Scott, surely you have some friends who disagree with her and still think naturalness a valid criterion for supersymmetry or want to say dark matter is reason enough and there is good reason to think next collider will find dark matter candidate in the energy range proposed.
Scott is such a talented guy in his field that he gets to meet the top talented people in other fields including HEP. They’ve become friends. Scott says he has no dog in any fight about BSM and I believe him. Still, his friends *do.* And the top people in the field of HEP overwhelmingly thought the LHC would see some new particles because of arguments from naturalness. That was the group consensus. It would be very surprising then if Scott *didn’t* have friends in HEP that were on the side of naturalness because nearly everyone was. So far they’ve been proven wrong.
I’m just shocked that none of those people are interested in publically rebutting Sabine if they still believe in naturalness or believe there is solid motivation for finding BSM at next collider. Their silence speaks volumes.
Comment #135 February 8th, 2019 at 10:49 am
Apologies again. Hangover got the better of me today.
Comment #136 February 8th, 2019 at 12:26 pm
Bunsen,
I think there’s a flaw in your theory. What do you think would happen if the government decided to finance a quadrillion dollars in new spending via new debt and money issuance?
Comment #137 February 8th, 2019 at 12:51 pm
Atreat #134
>And the top people in the field of HEP “overwhelmingly thought” the LHC would see some new particles because of arguments from naturalness. That was the group consensus. It would be very surprising then if Scott *didn’t* have friends in HEP that were on the side of naturalness because nearly everyone was. So far they’ve been proven wrong.
Not “overwhelmingly thought” but as far as I remember, and I was a part of the people planning experiments for the LHC, “overwhelmingly hoped” that new particles would be found, not just the Higgs, also supersymmetric, or , in my case the signature of large extra dimensions.
As far as I remember naturalness did not come into the discussions, just to see the Higgs and whether there was something beyond the standard model when we went to uncharted waters. We hoped. After all there are other models then strings: technicolor, possibility of deterministic models as Gerald ‘t Hooft has proposed. Whatever nature had to offer.
FCC will go into further uncharted waters and the whole gamut of theories will be there to be tested on real data. Theories fall by falsification and at the moment the field is open.
The LHC project certainly was pursued as a large experiment with open outcomes to chose between theories or generate new theories .
And LHC is breaking even in its return of the $ costs to society. And I predict that naturally the FCC will also do that 🙂 .
Comment #138 February 8th, 2019 at 1:17 pm
jonathan #136
Such a rapid explosion of the money supply would result in inflation until currency speculation stabilised the dollar at a new lower value to other currencies. Unless of course you are Japan in which case it might be the bare minimum to to keep them out of a deflationary spiral.
Comment #139 February 8th, 2019 at 2:31 pm
Atreat #134
>The question is whether [next generation collider] is worth $20 billion and the opportunity cost lost to other experiments. I’m sympathetic that we should do it. Sabine is not as sympathetic. People can disagree about this.
Fair points, indeed. In this vein, what would be your thoughts about how we should decide which discipline receive what share of the european, public investment in research?
Comment #140 February 8th, 2019 at 3:32 pm
Bunsen,
Good. So we agree that the government cannot magic resources out of thin air by printing money. But then I’m not sure how to interpret your statement that, due to the government’s ability to issue debt and currency, we do not need to worry about budget constraints.
Comment #141 February 8th, 2019 at 4:15 pm
Anna V #137
>Theories fall by falsification and at the moment the field is open.
Maybe you will agree that your field can be described as ‘already fallen short of good odds of discovering something with a new collider’. Scott mentioned 30% at best. Many think that’s even lower. If you think that’s better, can you explain how you compute your estimate? If not, don’t you think physicists have many projects that could be both more interesting and with better odds of success that the new collider you defend?
Comment #142 February 8th, 2019 at 5:19 pm
Scott #117
Suppose the “random number generator” is from a quantum source (like radioactive decay) and the events happen very rapidly (many times a second) so that there is no chance of “a quantum decoherence event” occurring – wouldn’t the “classical computer” now be in superposition until measured?
Comment #143 February 8th, 2019 at 5:46 pm
James #142: I don’t know if you appreciate just how rapidly decoherence happens for a typical macroscopic object. But if I’m not mistaken, the timescale for amplification would normally be no more than the time needed for light to propagate from one end of the object to the other end.
Comment #144 February 8th, 2019 at 6:10 pm
Scott #143
I agree, and it’s weird how Schrödinger’s Cat example got so popular, I guess that Quantum Mechanics was such a remarkable change from the classical viewpoint and we had WWII in between that it took a while for the modern decoherence theory to emerge.
However, we do have the question of how quick can the successive random jumps occur? If nature does them at planck timescales then everything is in superposition until we measure it.
And in this case it would still be a single path evolution – we just need to trust the mathematical formalism to guarantee all the QM outcomes we observe.
Comment #145 February 8th, 2019 at 7:03 pm
James #144: Schrödinger’s cat is fine as an example of macroscopic coherence, as long as we understand that it would have to be an extremely special cat, engineered using hypothetical technologies of the far future to not decohere. (Or maybe a simulation of a cat running on an error-correcting quantum computer.) Any cat you’ve ever seen would decohere almost instantly, becoming “definitely alive” or “definitely dead” relative to the observer (you), and placing it in a sealed box would make no difference to this.
Comment #146 February 8th, 2019 at 7:19 pm
Scott #145
er, yeah, I agreed about the cat, what about nature doing random jumps at planck timescales?
The point is, that if nature does the random “jumps” at planck timescales, it explains what we observe without many-worlds branching, and also gives us a light-speed limit, and also explains 3D space as a dynamical entity
Comment #147 February 8th, 2019 at 7:37 pm
James #146: I didn’t even understand what you mean about “nature doing random jumps at Planck timescales.” If you’re talking about a GRW-style dynamical decoherence mechanism, then the challenge is to keep such a mechanism from violating already-known experimental constraints, e.g. about quantum coherence that can in some cases persist for hours, or apply to systems nearly visible with the naked eye (though not yet both at once 🙂 ). “Random jump” theories also tend to do violence to Lorentz invariance, conservation of energy, and other symmetry principles that are central to known physics.
Comment #148 February 8th, 2019 at 8:06 pm
Scott #147
erm, no, those alt theories you mention are wrong, I’m talking about an idea that even Dirac mentioned at the famous 1927 Solvay Conference
“The particular ψ n that it shall be must be regarded as chosen by nature. One may say that nature chooses which ψ n it is to be, as the only information given by the theory is that the probability of any ψ n being chosen is |c n |^2 . The value of the suffix n that labels the particular ψ n chosen may be the result of an experiment, and the result of an experiment must always be such a number. It is a number describing an irrevocable choice of nature, which must affect the whole of the future course of events.”
Comment #149 February 8th, 2019 at 8:08 pm
Scott # 143:
>> “But if I’m not mistaken, the timescale for amplification would normally be no more than the time needed for light to propagate from one end of the object to the other end.”
No, I guess we are not that fortunate either.
The time needed for the propagation of light (i.e. the importance of the “c” limit) is pretty much an ensemble-based or macroscopic an idea.
But at least to a “first-order” approximation (I mean, according to the accuracy of the experimental bases of our QM postulates), QM does carry IAD (i.e., instantaneous action at a distance) as far as changes to the system wavefunction $\Psi(r,t)$ are concerned. Which means, in QM, the Fourier theory holds as a very basic and essential absolute. It is not just a close approximation that helps in calculations; it exists right at the core of the theory. At least in our present-day, arguably only “first-order”, QM theory. [And any “second-order” theory would still have to much respect the ideas in it!]
As a result, in QM, the Fourier components could always adjust themselves in such a way that one particle in effect pops out of existence at one end of a macroscopic object even as another one of the same kind appears at the other end, with the two events separated in time \Delta t <> c.
If similarly fast processes occur at enough points in the macroscopic object, and if these processes work in a way that furthers decoherence over that entire object, then the timescale required for the amplification you talk about could easily be << (cL).
Personally, I would like to know if someone has written a simple and easy-to-understand analysis of the expected decoherence times in objects like a QC that is also statistically well informed. … An analysis like that wouldn't just help the QC skeptic in furthering his argument; it would also come in useful to the QC enthusiast in picking out better architectures for his enterprise.
Best,
–Ajit
Comment #150 February 8th, 2019 at 8:22 pm
Scott #147
I spent so long looking for the Dirac quote from the 1927 Solvay Conference about nature doing all the quantum jumps, that I forgot that your scientific arguments against me are so poor – I’m talking about planck timescales
somebody help
Comment #151 February 8th, 2019 at 9:29 pm
@Scott #145
Indeed, I remember hearing of a presentation back in the 90’s titled “Le chat de Schrodinger est mort de décohérence”. I’ve taken that to mean that decoherence essentially solves the “measurement problem”, at least for any practical experiment.
Going back to the classical limit it’s interesting that that approach derives classical behavior without explicit reference to measurement. I take it that decoherence is again the mechanism (ie. a particle with a sufficiently short de Broglie wavelength essentially decoheres with itself).
Comment #152 February 9th, 2019 at 12:19 am
Jules-Pierre Mao #141
Falsification means that a contrary measurement has been made. This has not happened with the present HEP theories, because they do not predict hard numbers, but behaviors that can extend in energy with no mathematical contradictions.
You ask:
> Scott mentioned 30% at best. Many think that’s even lower. If you think that’s better, can you explain how you compute your estimate? If not, don’t you think physicists have many projects that could be both more interesting and with better odds of success that the new collider you defend?
Crossing frontiers one needs a map. The present theories do not have accurate maps. They are like medieval maps with “here there be dragons” or “here there be tigers” . All estimates must be qualitative. For experimental HEP physicists , it is enough to cross frontiers to *hope* for validations or falsifications of the theories used as maps, and also hope for something completely unexpected that will throw everything out on its ear 🙂 . We are explorers.
My *hopes* come from having crossed frontiers over these 55 years I am first, studying then working and then, as retired, contemplating the new proposals. Having watched the quark revolution and the emergence of the strong force theory and the discovery of the higgs validating the standard model, I would also say 30%. ( I have not given up hope in something emerging from the LHC data, people are still working on them).
Please read carefully this quote which should be a lesson for the detractors of the effort for the FCC , the monetary effect of cutting the SSC:
https://www.aps.org/publications/apsnews/201310/physicshistory.cfm
>The decision did not lead to increased funding for other areas of physics. In fact, the biggest beneficiary was the LHC, as the US particle physics community successfully lobbied for a greater role in the international collaboration. That investment paid off handsomely with the discovery of the Higgs boson.
It made no difference to the rest of the physics community money allocations, because politicians allocate money according to their own intuitions which depend on much larger sociological considerations, not really physics. Physicists have to put in good cost/benefit arguments, as I have been discussing in most of my posts.
A cost benefit for the LHC which I have linked above, shows a 95% return . Like any large government project, from cathedrals in the middle ages or the building spree to get out of the depression in the US, it gives jobs (and expertise and education in the case of LHC project estimate ) which are a monetary return to the community. ( They have not taken into account the large value added by the new technologies forced by the frontier project, that will be extra value added).
So this campaign against HEP new experiments will not enlarge the coffers of the rest of physics experiments, at least that is what happened with the SSC where a similar campaign to stop it did stop it.
The proposal to politicians should stand on the argument of *new frontiers to cross* and cost/benefit studies.
Comment #153 February 9th, 2019 at 3:14 am
Scott, FWIW, Sabine said in a comment on her blog that your definition of “almost tautologically true” naturalness was *exactly* an ideal example of the kind of arguments from beauty that she thinks has led HEP astray. Read her latest blog post about how people don’t even know they are using arguments from beauty because they think it so obviously true.
Comment #154 February 9th, 2019 at 4:03 am
Jonathon 140#
My point is that the government does not have a hidden piggy bank that it needs to break open to fund a new project. There do exist constraints on what it can do with the money supply without causing problems for the whole economy. However, you are talking about governments whose GDP is measure in trillions, and a process of investing several billion over many years. This is not something that is going to cause any degree of economic chaos, nor will it affect funding decisions in other areas, as these decisions will be based on different criteria.
Comment #155 February 9th, 2019 at 4:52 am
Atreat #153: Then Sabine and I fundamentally disagree. If I said, “supersymmetry basically has to be there because it’s such a beautiful symmetry,” that would be an argument from beauty. But I didn’t say that, and I disagree with anyone who does say it. I made something weaker, what you might call an argument from the explanatory coherence of the world. It merely says that, when we find basic parameters of nature to be precariously balanced against each other, to one part in 1010 or whatever, there’s almost certainly some explanation. It doesn’t say the explanation will be beautiful, it doesn’t say it will be discoverable by an FCC or any other collider, and it doesn’t say it will have a form (like SUSY) that anyone has thought of yet.
Separately, I do tend to be a fan of open-ended exploration to try to explain things that are currently unexplained, especially if there are obvious places to look where no one has looked yet. If I weren’t, I’d be in a different line of work. 🙂
Comment #156 February 9th, 2019 at 5:01 am
James #148 and #150: That Dirac quote (like many Dirac quotes) is beautiful and evocative, but it still doesn’t suggest a criterion for when a choice of Nature is actually “irrevocable,” for when there couldn’t even in principle be a recoherence. Saying that the splittings “happen at the Planck scale,” whatever that means (wouldn’t everything “happen at the Planck scale,” in the ultimate quantum theory of gravity?), is also not giving a criterion. Ultimately we need to know: if we do such-and-such experiment in the lab to create a Schrödinger-cat-like state, will we see “irrevocable splitting,” or will we still be able to observe interference between the branches if we’re careful enough? And if you ever answer “irrevocable splitting,” you’ve committed yourself to a clear prediction that differs from the prediction of orthodox QM, and that could in principle be tested.
But I fear we’re talking past each other, so let’s end this exchange.
Comment #157 February 9th, 2019 at 5:09 am
Everyone: I’m going to close this thread soon, because of lack of time on my part. But I wanted to call attention to a hilarious irony. For years, I’ve made the case that trying to build scalable quantum computers, in order to probe the universe for the first time in “the regime beyond the classical Extended Church-Turing Thesis,” is just as scientifically interesting as finding the Higgs boson—even if we set aside any of the possible applications of QC.
I don’t think I imagined to what extent the tables would someday turn—with funding now flowing into quantum information like beer at a frat party (for a combination of good and bad reasons…), with the future of experimental particle physics now in serious doubt, and with me put in the position of arguing that the high-energy frontier is worth exploring too! 😀
Comment #158 February 9th, 2019 at 7:25 am
Bunsen,
The extreme case illustrates the point, but the logic applies to smaller expenditures as well. Every dollar that the government spends must come from somewhere. This is clearest if you think in terms of physical resources: when the government finances the construction of a new super-collider, the physical materials and labor used in its construction are not available to other uses. This pushes up the prices of these inputs, raising the costs of other projects. This is called crowding out.
It’s true that this process isn’t very noticeable for a given project (even a multi-billion dollar one). But that is an illusion; it necessarily works in precisely the same way.
Now it’s true that under certain circumstances (e.g. during a recession) resources are underutilized and government expenditures are a “free lunch”, in the sense that they are redirected from uses of very low marginal value. But that circumstance does not apply in the US (though perhaps to a small degree in Europe); and if it did it would be best to address this directly with macroeconomic policy rather than using it to justify any particular expenditure.
The question, as ever, is whether a given government expenditure directs resources to a use of higher marginal social value than their alternative use. This should ideally be considered independent of considerations of macroeconomic stability and optimal government financing (timing of taxes vs. debt issuance, seigniorage, etc).
(As it happens, I’m an economics professor, so at least there’s one topic in this thread I can speak to with some authority 😉 of course, always happen to discuss further.)
Comment #159 February 9th, 2019 at 7:40 am
Anna V #152,
>I would also say 30%
Thanks for your estimate (I’d have guessed experts would agree on 3% at best, so I stand corrected).
>We are explorers.
That’s what most scientists think, including many physicists outside of your field, and even more outside of physics. This doesn’t change the need to fund the best projects.
Look, your field were once really well funded (not in absolute term but relative to what many other fields could get) and for good reasons (I was a big fan of the LHC myself, and sorry that the most boring scenario was the right one). At present, your field has 70% of chance of remaining dry of new non trivial data for the next few decades, even assuming a new collider, even by your own estimate. It’s time to notice that smart money is no longer on new colliders.
Comment #160 February 9th, 2019 at 1:45 pm
Jules-Pierre Mao #159
> It’s time to notice that smart money is no longer on new colliders.
In my post #152 , there is a quote about what happened with the money when SSC in the US was stopped.
>The decision did not lead to increased funding for other areas of physics. In fact, the biggest beneficiary was the LHC, as the US particle physics community successfully lobbied for a greater role in the international collaboration. That investment paid off handsomely with the discovery of the Higgs boson.
You , as many others, are confusing physics arguments, with the way ruling bodies allocate money for large projects. Physics is a small part,if any, of their interest. Cost/benefit is what they really decide on. at least up to now.
If the FCC falls through the ILC will get it, where the chance of new physics is smaller, or the one they are deciding in China.
https://www.nature.com/articles/d41586-018-07492-w
If with “smart money” you mean physicists and other scientists betting on a 30% chance will not do it?
I have again to quote Lord Kelvin ( and/ or others) who thought that physics was finished after the success or thermodynamics and electromagnetism:
““There is nothing new to be discovered in physics now. All that remains is more and more precise measurement.”
And then came the twentieth century physics.
Research in higher and higher energies in particle physics opens real frontiers, that may have unexpected results, as the results of nuclear physics were unexpected when they were discovered. ( The defense to the ruling bodies for building CERN did not rest on physics models, as there were really none at the time. It was the possibility of the use of new discoveries that the countries wanted to secure for themselves, in case of military applications !)
Comment #161 February 9th, 2019 at 3:11 pm
Scott #117 It might be ironic if in trying to build powerful QC machines, roadblocks and failures keep coming up which may be connected to the objections of the skeptics like Kalai. How long do you keep going with the engineering attempts here? Until the money runs out? 😉
Comment #162 February 9th, 2019 at 3:56 pm
Mike #161: Yes, until either you learn the truth or the money runs out. And I don’t think Gil disagrees!
Comment #163 February 9th, 2019 at 4:21 pm
I’ll make exactly the same argument as I made on Sabine’s blog.
1) Suppose we told the funding agencies what Sabine claims is the truth (and that I haven’t seen any credible sources disputing): with probability 90%, we find nothing except a few more decimal points for properties of the Higgs boson? Would the funding agencies build the next collider? I expect not.
2) So in order to build this, the particle physicists are going to have to lie, and promise axions, sterile neutrinos, extra dimensions, supersymmetric particles, and whatnot. Now, suppose we 30 billion dollars, and we see zilch? Is the backlash going to be good for particle physics? For physics in general? For big science? No! I don’t know how bad the backlash would be, but I really wouldn’t want to be proposing any even moderately big physics experiments after this happens.
So rather than setting ourselves up for a future physics funding disaster, we should just not build it.
The LHC didn’t have this problem, because either (a) it would see the Higgs, and learning the properties of the Higgs would be worth the money or (b) it wouldn’t see the Higgs, and that would be even more amazing than seeing it.
Comment #164 February 9th, 2019 at 6:18 pm
Scott #157
It’s maybe even sensible that the big collider projects get put on hold until we confirm we understand quantum mechanics, at least at the level of Quantum Computers to a few hundred qubits.
Imagine if we are in the middle of building a $100 billion dollar super-collider and all results from Quantum Computing experiments show that the theory breaks down at a few hundred qubits?
Quantum Computing is the area to target for a few years, if that succeeds we then should build the colliders, but ironically, if the theory is good enough, the next new particle might be discovered by a quantum computer simulation in any case
Comment #165 February 9th, 2019 at 6:26 pm
jonathan #158:
I don’t see the point in considering extreme cases. No one is trying to build a collider the size of the moon. As for the standard neoclassical argument about optimal resource allocation in an economy. That is a very different argument that is beyond what this comments section can allow. I am quite heterodox in my view on economics, and consider the typical necoclassical equilibrium models to be utter bullshit having zero relation to how a real economy functions.
Comment #166 February 9th, 2019 at 9:57 pm
Peter Shor #163: Here’s how I imagine the game theory from a particle physicist’s perspective:
1) If the FCC is built and finds nothing, there might be a backlash that spells the end of particle physics for quite some time (although I’m skeptical of that—I’ve worried for 20 years about irresponsible hype creating a backlash against QC, but so far it’s been only the opposite…).
2) Then again, if the FCC is built and finds nothing, that would probably spell the end of particle physics anyway for quite some time, even without such a backlash!
3) Meanwhile, if the FCC is built and finds something, then particle physics continues and we all rejoice over the decision to build.
4) If the FCC is not built, then particle physics (or at least the high-energy experimental frontier) effectively ends right now, or rather at the end of the LHC’s lifetime.
Under these circumstances, isn’t advocating for the FCC simply a dominant strategy from a particle physicist’s standpoint?
Comment #167 February 9th, 2019 at 11:35 pm
Let me tell you how decision would happen in Greece on whether to allocate funds , (straightened because of the economic crisis) for the FCC, and I am sure a similar thing would happen in the tens of countries that will have to take part in the FCC .
1) the FCC proposal has to be ready, submitted with a clear physics map/goal and a list of what the expected advantages are in education, in being allocated part of the build up, and also of the build up of the experiments, the transfer of knowledge. All in the framework of Greek education and industry.
2) The lobbying by group leaders of HEP groups on the politically appointed administrators on how this would enhance the profile of the current government internationally and also within Greece offering all the arguments for cost/benefit effects.
The whole thing hinges on convincing the administrator(or committee he/she has assigned) to advise the higher up politicians that it is profile enhancing among the voters and eventually a politically correct choice.
That is why, in my opinion it is important to have a clear cost/benefit study and not to lean too much on the physics but on the “going to a new frontier”.
It would be interesting to see a study/history of how the decision by the political bodies for building higher energy accelerators was taken at the time. We know about the SSC, and how the money did not go to other branches of physics but to different high energy experiments.
Comment #168 February 10th, 2019 at 1:34 am
Scott #166: Are we sure about 4? What if we don’t start building the FCC now but bring it up again in one or several decades? I don’t understand the relevant technology well enough to say, but is not plausible that, because of technological progress, postponing will allow us to reach even higher energies at the same cost (measured as a fraction of GDP), thereby increasing the chance we will find something?
Comment #169 February 10th, 2019 at 3:42 am
Vanessa #166
>I don’t understand the relevant technology well enough to say, but is not plausible that, because of technological progress,
Technological progress on accelerators comes from physicists and engineers working on accelerators. If we stop at the LHC, the current experts will retire and, after decades, one would have to start from scratch. The FCC utilizes older accelerators, these would have crumbled with the passing decades.
The flame has to be carried on, if one does not plan to reduce studying the basic structure of nature to history, and generate dark ages for the subject. If the FCC does not materialize the most probable result of scientists lobbying for higher energies will be for the money to go to ILC or the Chinese plan.
Comment #170 February 10th, 2019 at 3:59 am
Scott
Before you close the thread, let me state some science fiction scenaria of what could be there, around the corner in energy, and how it could really affect the world as we know it.
1) string theory is verified , this means that nature really has extra dimensions, 6 or 7.
2) large extra dimensions are verified
Science fiction:
This could, with extra theories and experiments , revolutionize communications, if one can cross into them with some of the extra gauge bosons of string theory: effectively the speed of light would be no problem if two locations are close in the extra dimension.
Extra dimensions could explain telepathy etc, and allow experimental control.
These are possibilities, improbable as viewed from our stand, but if Maxwell had not unified electricity and magnetism, would we be communicating on this site now?
Comment #171 February 10th, 2019 at 9:07 am
Anna V,
Let me tell you how folks at the European Commission proceeded last time. They announced their commitment to spend a few G euros for two big projects. They set up a public competition asking any scientist to present their preferred ones. They evaluated a few dozen and ended up funding the two bests (one for neuroinformatics, one for graphen). If FCC could survive this kind of process, you’d probably have my vote. But patronizing arguments doesn’t help you’re beating a dead horse. It won’t walk again. Sorry!
Comment #172 February 10th, 2019 at 10:35 am
Scott#166:
Good point. But it’s only a dominant strategy if the particle physicist doesn’t care about messing up the funding for other areas of experimental physics.
I’ll let individual particle physicists decide how they feel about that.
Comment #173 February 11th, 2019 at 8:33 am
Jules-Pierre Mao #171
CERN is funded by individual countries, NOT the European Union. There is no “call for proposals” there is just lobbying within the countries.
Comment #174 February 11th, 2019 at 12:04 pm
The solution is obviously to use crowd funding…
More seriously, I doubt that the actual true cost of this thing would be a mere 20 billion$ (http://blog.u2ec.org/wordpress/?p=2082)
Comment #175 February 11th, 2019 at 7:33 pm
Peter Shor #163: “Suppose we told the funding agencies what Sabine claims is the truth (and that I haven’t seen any credible sources disputing): with probability 90%, we find nothing except a few more decimal points for properties of the Higgs boson?”
According to Sabine’s anti-naturalness arguments, such a probability is impossible to compute or even estimate.
Comment #176 February 12th, 2019 at 2:30 pm
Even though we only got the Higgs (so far), the LHC was well worth the price. The Higgs particle is basically a patch to ensure mathematical consistency in the standard model. Remarkably, it is actually there.
Here’s a question – does anyone really believe that 20 billion will really get us a 100 Tev collider?
Comment #177 February 15th, 2019 at 8:49 pm
[…] some comments from Scott Aaronson on the current “like beer at a frat party” state of funding of quantum information […]
Comment #178 February 16th, 2019 at 8:00 am
I read through the posting and all the comments and it seems to me that too many people are missing the point. Before we commit to FCC, we need to measure the parameters of particles we already know about better. LHC is not good at measuring the properties of the Higgs, for example, because p+p- collisions are inherently messy. e+e- collisions are much cleaner, but the LEP (in the same tunnel as the LHC) was limited to 300 GeV by synchrotron losses. It seems to me that the proper way forward for those arguing for the FCC is to push for construction of the ILC as a priority (cost estimated as 7.78 billion 2012$) and then use results from it to make the case for the FCC as a hadron collider. To simply make the jump in scale based on arm-waving arguments from theorists that it must find new physics is not good science.
Comment #179 February 16th, 2019 at 8:34 am
Dr. Aaronson,
your argument against Dr. Hossenfelder’s position reminds me of a story:
Elementary school.
Teacher: “Bobby, if you have 6 apples and divide them up with your brother, how much do you have then?”
Bobby: “One.”
Teacher: “Looks to me like you don’t know mathematics.”
Bobby: “Looks to me like you don’t know my brother.”
……………..
Comment #180 February 17th, 2019 at 10:47 am
Laurence C #178
The FCC will start with what the ILC aims to do, e+e- collisions around the Higgs
“The FCC examines scenarios for three different types of particle collisions: hadron (proton-proton and heavy ion) collisions, like in the LHC; electron-positron collisions, as in the former LEP; and proton-electron collisions.”
https://home.cern/science/accelerators/future-circular-collider
As happened with LEP, where the energy region explored was up to 210 GeV , and in the same tunnel the LHC was introduced. Conservation of tunnels :).
see https://cds.cern.ch/record/2651299?ln=en
Comment #181 February 17th, 2019 at 11:19 am
Ned #179: Your story had no relation to anything that I could discern. Are you sure you’re not a chatbot? (Or maybe the new super-advanced babbler from OpenAI?) 🙂
Comment #182 February 17th, 2019 at 10:02 pm
Scott wrote:
Do you know examples of this sort of situation in particle physics, or is this just a hypothetical situation?
Comment #183 February 18th, 2019 at 7:18 am
John Baez #182: To answer a question with a question, do you disagree that that’s the current situation with (for example) the Higgs mass, not to mention the vacuum energy, if one considers everything that could naïvely contribute? A lot of people told me it was, but maybe they lied or I misunderstood them.
Comment #184 February 18th, 2019 at 2:32 pm
Scott #183:
The basic rough story is this. We measure the Higgs mass. We can assume that the Standard Model is good up to some energy near the Planck energy, after which it fizzles out for some unspecified reason.
According to the Standard Model, each of the 25 fundamental constants appearing in the Standard Model is a “running coupling constant”. That is, it’s not really a constant, but a function of energy: roughly the energy of the process we use to measure that process. Let’s call these “coupling constants measured at energy E”. Each of these 25 functions is determined by the value of all 25 functions at any fixed energy E – e.g. energy zero, or the Planck energy. This is called the “renormalization group flow”.
So, the Higgs mass we measure is actually the Higgs mass at some energy E quite low compared to the Planck energy.
And, it turns out that to get this measured value of the Higgs mass, the values of some fundamental constants measured at energies near the Planck mass need to almost cancel out. More precisely, some complicated function of them needs to almost but not quite obey some equation.
People summarize the story this way: to get the observed Higgs mass we need to “fine-tune” the fundamental constants’ values as measured near the Planck energy, if we assume the Standard Model is valid up to energies near the Planck energy.
A lot of particle physicists accept this reasoning and additionally assume that fine-tuning the values of fundamental constants as measured near the Planck energy is “bad”. They conclude that it would be “bad” for the Standard Model to be valid up to the Planck energy.
(In the previous paragraph you can replace “bad” with some other word – for example, “implausible”.)
Indeed you can use a refined version of the argument I’m sketching here to say “either the fundamental constants measured at energy E need to obey an identity up to precision ε or the Standard Model must break down before we reach energy E”, where ε gets smaller as E gets bigger.
Then, in theory, you can pick an ε and say “an ε smaller than that would make me very nervous.” Then you can conclude that “if the Standard Model is valid up to energy E, that will make me very nervous”.
(But I honestly don’t know anyone who has approximately computed ε as a function of E. Often people seem content to hand-wave.)
People like to argue about how small an ε should make us nervous, or even whether any value of ε should make us nervous.
But another assumption behind this whole line of reasoning is that the values of fundamental constants as measured at some energy near the Planck energy are “more important” than their values as measured near energy zero, so we should take near-cancellations of these high-energy values seriously – more seriously, I suppose, than near-cancellations at low energies.
Most particle physicists will defend this idea quite passionately. The philosophy seems to be that God designed high-energy physics and left his grad students to work out its consequences at low energies – so if you want to understand physics, you need to focus on high energies.
Comment #185 February 19th, 2019 at 11:26 am
John #184: One reason many of us think this philosophy isn’t unreasonable is that we have precedent for it in physics: this is how we pretty much understand all of material science. In condensed matter physics we know the full theory of everything: atoms interacting via electromagnetic interactions, described via a non-relativistic Schrodinger equation. Indeed, the microscopic physics is here the more fundamental one: at atomic scales you know what your material is made off. Here all constants you put in your Hamiltonian are the fundamental constants of nature (the fine structure constant, the mass of the nuclei and the electron) and all couplings are of order 1. No artificially small numbers. Even all factors of 100 that show up can be understood as powers of the fine-structure constant – the small parameter in the problem.
Now if you look at a generic material you can use “naturalness” to figure out that light fermions can describe quite generic materials (metals!) since they don’t require fine tuning, but light bosons only should happen if we fine tune microscopic constants (at phase transitions, where you dialed at least one parameter to a special value). And this beautifully agrees with experiment. Making this more quantitative you arrive at Fermi liquid theory and Landau’s theory of phase transitions, the cornerstones of modern condensed matter physics. So at least in one area of physics (an area much larger than all of particle physics for sure) “naturalness” is stunningly successful.
Now as far as particle physics is concerned we have the problem that we only have one world, so we can not in fact dial the microscopic parameters. But it was certainly not unreasonable to imagine that maybe naturalness should apply in this case to. It’s not an open and shut case, never was. But it’s a working hypothesis whose experimental consequences should be worked out and tested. That program looks like it is pretty much complete and gave an answer (modulo loopholes). But that doesn’t make naturalness retroactively a bad idea, and doesn’t take away any of its stunning successes in other areas of physics.
Comment #186 February 20th, 2019 at 2:23 pm
Andreas #183 – can you list some of the “stunning successes of naturalness”? Were the Fermi liquid theory and Landau’s theory of phase transitions discovered via considerations of naturalness? I don’t remember hearing about that.
Comment #187 February 21st, 2019 at 11:24 am
John #184:
“Were the Fermi liquid theory and Landau’s theory of phase transitions discovered via considerations of naturalness?”
Yes.
Landau didn’t call it naturalness, but it’s the same idea. You need to fine-tune microscopic parameters to get light bosons. You get light fermions for free. It’s the basic insight that underlies all of modern condensed matter physics.
Again, that doesn’t mean it has to apply to particle physics. Apparently it doesn’t. But it is a very powerful way to organize our thinking in areas of physics where we can actually dial microscopic parameters.
Comment #188 February 22nd, 2019 at 3:32 am
@Andreas Karch: Can you explain a bit more what you mean by getting light fermions for free, and getting light bosons only if you fine tune microscopic constants? I guess the starting point is QFT with the fine structure constant at 1/137 being sufficiently natural. Next we get electrons as light fermions, the bare atomic nuclei with an odd number of nucleons as heavy fermions, and the bare atomic nuclei with an even number of nucleons as heavy bosons.
First question: what about the photon? Does it count as a light boson? Is it excluded from the statement, because it is already contained in QFT, the starting point? Or is it actually included in the statement, because it has no mass at all, and QFT would not even allow a light boson to start with (as explained above, QFT obviously did allow heavy bosons and both light and heavy fermions to start with).
Then we come to the common quasi-particles in condensed matter physics. We have phonons and plasmons, which are both bosons. It is a bit unclear whether plasmons are light or heavy, but at least their lifetime is quite short, which could mean that they are heavy. Since phonons can completely change the momentum of an electron in an interaction without transfering much energy, they should definitively considered to be heavy.
Then we have the fermi liquid theory, in which we get fermionic quasi-particles, like the electrons and holes near the fermi-surface in typical (non-magnetic) metals, or nearly keep the original fermions in cases like Liquid helium-3. The lifetime of the quasi-particles (in the first case) gets very short the farer away they are from the fermi surface. Not sure whether this should count as being heavy in this case, but even if it did, they are still fermions, and the statement said nothing against heavy fermions.
So where could you find light bosons in condensed matter physics, if you fine tune microscopic constants? In low temperature superconductivity, electrons from Cooper pairs, which are bosons. Are those bosons light or heavy? I don’t know. And if they are light, which is the microscopic constant that you tuned to get them?
Comment #189 February 23rd, 2019 at 10:27 am
gentzen, #188: You are of course absolutely right that we do know a few reasons for bosons to be light. The photon is a gauge boson. So it is naturally light. Note that you would never hear a particle physicist complain that a light photon is unnatural. We also don’t complain about light pions. That’s because they are (almost) Goldstone bosons of a broken symmetry. Same for the phonons (broken translations). But Goldstone bosons are very special, they can only derivatively couple. You know it when you see one. What is “unnatural” (that is requires fine tuning of microscopic parameters) in particle physics is only the Higgs. What’s the condensed matter analog of this? The fluctuations of order parameters near a phase transition. These fluctuations are generically heavy and irrelevant for the dynamics. When they are light, they give rise to interesting physics (critical phenomena, scaling exponents). But to get them light, you need to finetune (dial at least one parameter, a coupling or the temperature) to get yourself to the critical point. So Landau’s Fermi liquid = naturally light fermions. Landau’s theory of phase transitions = fine tuned light bosons. Again, Landau didn’t use this language. But he clearly knew about the basic physics behind this.
Comment #190 February 23rd, 2019 at 10:34 am
So you can think about the “naturalness” problem as: why is the Higgs boson living near a phase transition? Of course one possible answer is: why not?
Comment #191 February 25th, 2019 at 4:28 pm
[…] is a conversation I had with Scott Aaronson. It started on his blog, in a discussion about ‘fine-tuning’. Some say the Standard Model can’t be the […]
Comment #192 February 25th, 2019 at 4:33 pm
Scott and I moved our discussion of particle physics over to email, but we agreed it would be fun to let everyone read it. So, you can see it here:
• Problems with the Standard Model Higgs
Comment #193 February 25th, 2019 at 8:39 pm
I do appreciate Sabine’s argument, but for me it boils down to this: It’s science, and in science we always look. I don’t really understand an argument that suggests scientists shouldn’t look.
Comment #194 March 9th, 2019 at 9:26 am
[…] More here. […]
Comment #195 March 16th, 2019 at 11:35 pm
Scott #37: I read your 4-point summary of Dr. Hossenfelder’s position, moved on to your dissent, and pulled up short at the word ‘punish’. I hadn’t noticed anything looking like punishment in those four points, and I didn’t see it when I reread them. I haven’t read everything Sabine has written on the topic, but I don’t recall anything that struck me as being along those lines, just a claim that no particularly good case has been made for a bigger accelerator.
I am not particularly taken by your interstellar “I’ve got a bigger…” competition, either – wouldn’t a list of discoveries be a better yardstick? And the thing about the ‘what else would we do?’ argument is that it brings us back to another of Sabine’s issues – a shortage of testable grand hypotheses.
It is something of a cop-out to say that we should do it if money were no object – to be consistent, we should also take into consideration all the other ‘if money were no object’ projects, but then, of course, money would be an issue.
Comment #196 March 18th, 2019 at 12:05 pm
Scott #181: “Your story had no relation to anything that I could discern.”
Sorry for replying so late.
Dr. Aaronson, you confirm my impression:
As much as I love to read your blog and its (mainly) well-founded arguments, here you don’t see the situation … “Lost in Math” seems to be more appropriate than I thought.
Ok, the message of #179 spelled out:
You know logic – she knows physics.
Logically your arguments are ok, but they don’t have much to do with reality;
the reality she is facing and you aren’t.
You’re just voicing your empty thoughts here about something which is not really a concern to you – Dr. Hossenfelder is talking out of experience about her field, which is her life, where she is working, and deeply committed.
That’s a world of a difference; not only as a scientist but as a human being you should be aware of that.
🙁
Comment #197 March 18th, 2019 at 3:34 pm
Ned #196: Your argument is self-defeating. If experience in the field trumped mere logic, then there are thousands of physicists whose “real-world experience” with HEP phenomenology is much, much greater than Sabine’s, and they overwhelmingly disagree with her and support building a new collider. Sabine’s entire case—one that I don’t at all dismiss for this reason, but respect and try to answer!—is one about logic trumping experience, since she regards the most experienced people as compromised by groupthink and bias.
Or is that just yet more logic, which therefore doesn’t carry weight with you? 😉
Comment #198 March 20th, 2019 at 11:37 am
Dr. Aaronson,
thank you for taking your time to respond. I really appreciate that you are sharing your thoughts with the world – that is also why I take the trouble of writing to you, to give something back, if possible; otherwise who cares ? 😉
Where did I say that logic doesn’t carry any weight with me? It ‘s got its own place, where it works beautifully, as you yourself prove again and again – that’s why I’m reading your blog, you’re much better at it than I could ever dream to be, so I prefer to consult someone who knows what he’s talking about.
And that leads to the problem here:
Logic is absolutely fantastic, only one has to know where and when to apply it, and where and when its usefulness stops – that’s the hard part, especially when one has been so successful with it. So it’s easy to forget that it is only a – tiny – part of life. And with our society-wide general preoccupation with logic it becomes even harder to even see that fact.
Actually my argument 😉 would be better put like this:
In your posting you are arguing for something you do not really care about, at best in a superficial way, while Dr. Hossenfelder really cares about this. And you seem to be so caught up in arguments that you do not notice that.
Check it yourself: imagine if the situation were reversed, if you were talking about something you really care about and have invested you work in it for many years, then think with what completely different background you would be talking.
Disregarding such things leads to people of all kinds, scientists of course no exception, to start spouting nonsense when they’re out of their depth and don’t notice that. And I’m talking out of experience 🙁 .
Dr. Hossenfelder, whom I also very much respect (and regularly read her blog, too), is of course not immune to that – she’s human,too, after all ;), but that does not alter the fact that nonsense is nonsense, no matter who utters it.
This is put in a not very mellow way intentionally, to drive home 😉 my point, so please, Dr. Aaronson, don’t be offended but first have a look if there ma be some truth in what I’m saying.
If not, you’ll safely disregard it, and if there is – well, that’s up to you of course.
I hope I could make myself clearer, if not and if you should be interested enough to try again ;), I’ll look here again in the next days. In any case thank you once more for taking the time to converse on the net with someone who’s a complete stranger to you; I am really grateful for your kindness and openness. And that’s not a polite formula only.
Comment #199 July 1st, 2019 at 1:30 pm
[…] Hossenfelder—known to readers of Shtetl-Optimized for opposing the building of a higher-energy collider, or various other things—has weighed in on quantum supremacy in […]
Comment #200 August 9th, 2019 at 8:57 am
Here is Carlo Rubbia making the argument for a muon-collider as a Higgs factory in Quanta: https://www.quantamagazine.org/carlo-rubbia-calls-for-courage-as-physicists-confront-collider-dilemma-20190807/