 |
| [Image Source] |
1. The “Just look” argument.
This argument goes: “We don’t know that we will find something new, but we have to look!” or “We cannot afford to not try.” Sometimes this argument is delivered with poetic attitude, like: “Probing the unknown is the spirit of science” and similar slogans that would do well on motivational posters.
Science is exploratory and to make progress we should study what has not been studied before, true. But any new experiment in the foundations of physics does that. You can probe new regimes not only be reaching higher energies, but also by reaching higher resolution, better precision, bigger systems, lower temperatures, less noise, more data, and so on.
No one is saying we should stop explorative research in the foundations of physics. But since resources are limited, we should invest in experiments that bring the biggest benefit for the projected cost. This means the higher the expenses for an experiment, the better the reasons for building it should be. And since a bigger particle collider is presently the most expensive proposal on the table, particle physicists should have the best reasons.
“Just look” certainly does not deliver any such reason. We can look elsewhere for lower cost and more promise, for example by studying the dark ages or heavy quantum oscillators. (See also point 18.)
2. The “No Zero Sum” argument.
“It’s not a zero sum game,” they will say. This point is usually raised by particle physicists to claim that if they do not get money for a larger particle collider, then this does not imply a similar amount of money will go to some other area in the foundations of physics.
This argument is a badly veiled attempt to get me to stop criticizing them. It does nothing to explain why a particle collider is a good investment.
3. Everyone gets to do their experiment!
This usually comes up right after the No-Zero-Sum-argument. When I point out that we have to decide what is the best investment into progress in the foundations of physics, particle physicists claim that everyone’s proposal will get funded.
This is just untrue.
Take the Square Kilometer Array as an example. Its full plan is lacking about $1 billion in funding and the scientific mission is therefore seriously compromised. The FAIR project in Germany likewise had to slim down their aspirations because one of their planned detectors could not be accommodated in the budget. The James Webb Space telescope just narrowly escaped a funding limitation that would have threatened its potential. And that leaves aside those communities which do not have sufficient funding to even formulate proposals for large-scale experiments. (See also point 19.)
Decisions have to be made. Every “yes” to something implies a “no” to something else. I suspect particle physicists do not want to discuss the benefit of their research compared to that of other parts of the foundations of physics because they know they would not come out ahead. But that is exactly the conversation we need to have.
4. Remember the Superconducting Super Collider!
Yes, the Superconducting Super Collider (SSC). I remember. The SSC was planned in the United States in the 1980s. It would have reached energies somewhat exceeding that of the Large Hadron Collider, and somewhat below that of the now planned Future Circular Collider.
Whatever happened to the SSC? What happened is that the estimated cost ballooned from $5.3 billion in 1987 to $10 billion in 1993, and when US congress finally refused to eat up the bill, particle physicists collectively blamed Phillip Anderson. Anderson is a Nobel Prize winning condensed matter physicist who testified before the US congress in opposition of the project, pointing out that society doesn’t stand much to benefit from a big collider.
While Anderson’s testimony certainly did not help, particle physicists clearly use him as a scapegoat. Anderson-blaming has become a collective myth in their community. But historians largely agree the main reasons for the cancellation were: (a) the crudely wrong cost estimate, (b) the end of the cold war, (c) the lack of international financial contributions, and (d) the failure of particle physicists to explain why their mega-collider was worth building. Voss and Koshland, in a 1993 Editorial for Science, summed the latter point up as follows:
“That particle physics asks questions about the fundamental structure of matter does not give it any greater claim on taxpayer dollars than solid-state physics or molecular biology. Proponents of any project must justify the costs in relation to the scientific and social return. The scientific community needs to debate vigorously the best use of resources, and not just within specialized subdisciplines. There is a limited research budget and, although zero-sum arguments are tricky, researchers need to set their own priorities or others will do it for them.”Remember that?
5. It is not a waste of money
This usually refers to this attempted estimate to demonstrate that the LHC has a positive return on investment. That may be true (I don’t trust this estimate), but just because the LHC does not have a negative return on investment does not mean it’s a good investment. For this you would have to demonstrate it would be difficult to invest the money in a better way. Are you sure you cannot think of a better way to invest $20 billion to benefit mankind?
6. The “Money is wasted elsewhere too” argument.
The typical example I hear is the US military budget, but people have brought up pretty much anything else they don’t approve of, be that energy subsidies, MP salaries, or – as Lisa Randall recently did – the US government shutdown.
This argument simply demonstrates moral corruption: The ones making it want permission to waste money because waste of money has happened before. But the existence of stupidity does not justify more stupidity. Besides that, no one in the history of science funding ever got funding for complaining they don’t like how their government spends taxes.
The most interesting aspect of this argument is that particle physicists make it, even make it in public, though it means they basically admit their collider is a waste of money.
7. But particle physicists will leave if we don’t build this collider.
Too bad. Seriously, who cares? This is a profession almost exclusively funded by taxes. We don’t pay particle physicists just so they are not unemployed. We pay them because we hope they will generate knowledge that benefits society, if not now, then some time in the future. Please provide any reason that continuing to pay them is a good use of tax money. And if you can’t deliver a reason, I full well think we can let them go, thank you.
8. But we have unsolved problems in the foundations of physics.
This argument usually refers to the hierarchy problem, dark matter, dark energy, the baryon asymmetry, quantum gravity, and/or the nature of neutrino masses.
The hierarchy problem is not a problem, it is an aesthetic misgiving. For the other problems, there is no reason to think a larger collider would help solving them.
I have explained this extensively elsewhere and don’t want to go into the question what problems make promising research directions here. If you want more details, read eg this or this or my book.
9. So-and-so many billions is only such-and-such a tiny amount per person per day.
I have no idea what this is supposed to show. You can do the same exercise with literally any other expense. Did you know that for as little a tenth of a Cent per year per person I could pay my grad student?
10. Tim Berners-Lee invented the WWW while employed at CERN.
By the same logic we should build patent offices to develop new theories of gravitation.
11. It may lead to spin-offs.
The example they often bring up is contributions to WiFi technology that originated in some astrophysicists’ attempt to detect primordial black holes.
In response, allow me to rephrase the spin-off-argument: Physicists sometimes don’t waste all money invested into foundational research because they accidentally come across something that’s actually useful. That wasn’t what you meant? Well, but that’s what this argument says.
If these spin-offs are what you are really after, then you should invest more into data analysis or technology R&D, or at least try to find out which research environments are likely to benefit spin-offs. (It is presently unclear how relevant serendipity is to scientific progress.) Even in the best case this may be an argument for basic research in general, but not for building a particle collider in particular.
12. A big particle collider would benefit many tech industries and scientific networks.
Same with any other big investment into experimental science. It is not a good argument for a particle collider in particular.
13. It will be great for education, too!
If you want to invest into education, why dig a tunnel along with it?
14. Knowledge about particle physics will get lost if we do not continue.
We have scientific publications to avoid that. If particle physicists worry this may not work, they should learn to write comprehensible papers. Besides, it’s not like particle physicists would have no place to work if we do not build the next mega-collider. There are more than a hundred particle accelerators in the world; the LHC is merely the largest one. Also note that the LHC is not the only experiment at CERN. So, even if we do not build a larger collider, CERN would not just close down.
15. Highly energetic particle collisions are the cleanest way to measure the physics of short distances.
I tend to agree. This is what originally sparked my interest in high energy particle physics. But there is currently no reason to think that the next breakthroughs wait on shorter distances. Times change. The year is 2019, not 1999.
16. Lord Kelvin also said that physics was over and he was wrong
Yeah, except that I am the one saying we could do better things with $20 billion than measuring the next digits of some constants.
17. Particle accelerators are good for other things.
The typical example is that beams of ions can treat certain types of cancer better than the more common radiation therapies. That’s great of course, and I am all in favor of further developing this technology to enable the treatment of more patients, but this is an entirely different research avenue than building a larger collider.
18. You do not know what else we should do.
Sure I do. I wrote a whole book on this: In the foundations of physics, we should focus on those areas where we have inconsistencies, either between experiment and theory, or internal inconsistencies in the theories. Examining such inconsistencies is what has historically led to breakthroughs.
We currently have such situations in the following areas:
(a) Astrophysical and cosmological observations attributed to dark matter. These are discrepancies between theory and data which should be studied closer, until we have pinned down the theory. Some people have mistakenly claimed I am advocating more direct detection experiments for certain types of dark matter particles. This is not so. I am saying we need better observations of the already known discrepancies. Better sky coverage, better resolution, better stats. If we have a good idea what dark matter is, we can think of building a collider to test it, if that turns out to be useful.
(b) Quantum Gravity. The lack of a theory for quantized gravity is an internal theoretical inconsistency. We know it requires solution. A lot of physicists are not interested in experimentally testing this because they think it is not possible. I have previously explained here and here why that is wrong.
(c) The foundations of quantum mechanics: The measurement postulate is inconsistent with reductionism. There is basically no phenomenological or experimental exploration of this.
Needless to say, I think my argument for how to break the current impasse is a good one, but I do not really expect everyone to just agree with it. I am primarily putting this forward because it’s the kind of discussion we should have: We have not made progress in the foundations of physics for 40 years. What can we do about it? At least I have an argument. Particle physicists do not.
19. But you do not have any other worked-out proposals
The proposal for the FCC was worked out by a study group over 5 years, supported by 11 million Euro. Needless to say, I cannot, as a single person and in a few weeks of time, produce comparable proposals for large scale experiments. Expecting me to do so is unreasonable.
20. But it will do all these things
Particle physicists like to point towards their 716 pages report that summarizes what they could do with the FCC. But, look, no one doubts that you can do something with $20 billion. The question is whether what you can do is worth the investment. The report does not address this point at all.
Final sentence of 16.b) "I have previously written explained here and here why that is wrong." - I guess links are missing.
ReplyDeleteThanks for pointing out, I have fixed that.
DeleteHi Sabine,
ReplyDeleteI totally appreciate what you're doing, and it even opened my eyes to the systematic errors that scientists make. Please don't let the cargo cult followers silence you :)
But, as reader of your blog, I kinda miss the variety of the content that you published some time ago. Like reviews of new (or old) papers, introductions to new (and old) theories, etc.
I hope at some point you will get back to digging out such papers and theories, and presenting them...
Best regards
-Michael
Michael,
DeleteYes, I am aware of this :( I hope to get back to "normal" soon. I have several interesting papers I want to write about, but I am severely behind.
"The foundations of quantum mechanics: The measurement postulate is inconsistent with reductionism. There is basically no phenomenological or experimental exploration of this." At the start of the Quantum Information/Computing/Communication industry, it was very much felt that such things were experimental foundations of physics, and I think they were instrumental in making QM seem much more familiar than it felt before, say, 2000, whether we can say we now better understand measurement or not.
ReplyDeleteBy now many people working on such things would hate to be thought so impractical, and therefore probably wasting $billions, but the early runners went to Foundations of QM conferences and did care about such things. If quantum computation doesn't pan out quickly, perhaps we'll be treated to stories of how the many billions spent led to better understanding of the foundations of QM.
16. (d) The foundations of interacting QFT. We don't understand interacting QFT. [But you may remember that I'm as much a broken record on this as other people are about their enthusiasms.]
Peter,
DeleteYes, you are right. I should have included QFT in that. I usually do, but somehow I forgot. My bad.
"By the same logic we should build patent offices to develop new theories of gravitation." Not the worst logic of the arguments considered.
ReplyDeleteBefore you get annoyed about humanity spending money to advance fundamental knowledge consider this.. Google make $4 Billion/month from people clicking on their silly little ads. Give science a break. Give them the money. Lets look inside the proton. Unless of course you prefer to click on ads.
ReplyDelete1, 6 and sort of 9.
Delete@Richard " The Hossenfelder Scale" for measuring Crackpots is way better than The Baez's Crackpots Index ...
DeleteFor all who are discouraged to build the FCC (or CLIC) after reading the arguments above, I recommend to read the interview with Nima Arkani-Hamed, it will cheer you up again ! Where there is hope, there is life !
ReplyDeletehttps://cerncourier.com/in-it-for-the-long-haul/
If anyone can flesh out just a little what Sabine means by "the measurement postulate is inconsistent with reductionism," I'd be grateful.
ReplyDeleteI assume this is a problem I've heard stated in other terms, and I'm just failing to translate it into this phrasing. My failure, not Sabine's.
It is fleshed out here.
DeleteDave M,
DeleteThe point is that we would like our measurement instruments to be describable, in principle, by quantum mechanics. In that case, the measurement process should not require an additional assumption: all the details of the measurement process should be explained by QM without an additional measurement postulate.
If that is not so -- i.e., if the action of measurement instruments cannot be explained by QM alone -- then we are entitled to ask what novel physical process is going on in the measurement process that is not explained by quantum mechanics.
Weinberg explained this quite clearly in Sabine's interview in her book. See also his discussion in the second edition of his Lectures on Quantum Mechanics:
"If quantum mechanics applies to everything, then it must apply to a physicist’s measurement apparatus, and to physicists themselves. On the other hand, if quantum mechanics does not apply to everything, then we need to know where to draw the boundary of its area of validity. Does it apply only to systems that are not too large? Does it apply if a measurement is made by some automatic apparatus, and no human reads the result?"
The ultimate issue is whether (human?) consciousness somehow is needed to bring about a true measurement. Wigner suggested just that in his famous essay in The Scientist Speculates.
Of course, if it were ever shown that consciousness is integral to the measurement process, then we would be obligated to turn our attention to understanding consciousness, which would certainly be a change of direction for physics!
It seems reasonable that physicists should at least try to give a fully complete physical exposition of QM without invoking consciousness.
Weinberg sums up by alluding to perhaps the oddest aspect of this whole matter:
"Indeed, many physicists are satisfied with their own interpretation of quantum mechanics. But different physicists are satisfied with different interpretations."
So, if you think you know the "obvious" answer to Weinberg's questions, be aware that many physicists agree that there is an "obvious" answer, but they disagree as to what that "obvious" answer is.
Dave Miller
PhysicistDave,
DeleteI totally endorse what you have written above. I guess quite a lot of non-HEP scientists feel that there is unfinished business at the level of ordinary QM, and indeed that that may be truly fundamental.
As you point out, Shroedinger's equation properly applies to every part of life - not just a few particles that happen to be under study. Superficially those equations would imply a reality consisting of an ever more entangled wave function encompassing different possible situations superimposed.
The possible relationship between QM and consciousness clearly interests Roger Penrose, so there it isn't as though this idea has been 'settled', it has just been put to one side because it is embarrassing!
Physicist Dave,
DeleteIt seems reasonable that physicists should at least try to give a fully complete physical exposition of QM without invoking consciousness.
QM is a mathematical method for describing the statistical outcomes of otherwise unobservable physical processes. The math neither describes nor explains those processes. Why then, should we expect a complete physical exposition of QM (with or without consciousness)?
Bud Rap wrote,
Delete"QM is a mathematical method for describing the statistical outcomes of otherwise unobservable physical processes."
That makes QM sound like classical statistical mechanics, which I think isn't fair.
First of all, QM computes the wave function, which is *not* in itself a probability distribution - not least because it can take on negative or complex values.
QM isn't creating a statistical outcome of a deeper theory (although OK it is an approximation to QFT).
You only get probabilities when you evaluate Ψ Ψ*.
Surely physics should be more than obtaining some equations that seem to describe reality, shouldn't it also provide an explanation of what it is that the maths relates to?
"QM isn't creating a statistical outcome of a deeper theory (although OK it is an approximation to QFT)."
DeleteActually, it might as well be; it's just that we don't know that deeper theory yet. And I think even QFT doesn't fix that - you get a distribution over configurations of classical fields instead than over configurations of classical point-like particles, but the 'statistical distribution' effect remains.
David Bailey,
DeleteThat makes QM sound like classical statistical mechanics, which I think isn't fair.
At the interface between QM and observation statistics is all you get. That QM arrives there via a different set of formalisms necessitated by the peculiar circumstances of the quantum scale, doesn't alter the analogous nature of the outcome.
Surely physics should be more than obtaining some equations that seem to describe reality, shouldn't it also provide an explanation of what it is that the maths relates to?
It certainly should! My point was only that you cannot expect to obtain reasonable physical explanations from mathematical formalisms that aren't constructed on reasonable qualitative foundations.
Simone said,
Delete"Actually, it might as well be; it's just that we don't know that deeper theory yet. "
Well unless there are an infinite number of theories, each depending on the one below, the process has to stop somewhere. My gut feeling is that QM is special - it says that fundamentally we have different possibilities (realities if you like) that evolve and interfere with each other. This feels more fundamental than particles. So I would rate QM as fundamental, and since QM cannot coexist with GR, I'd bet that GR has to change.
Bee,
ReplyDeletehas Moriond 2019 found any BSM physics signals, i understand possible lepton flavor violations
Moriond is really only the occasion on which rumors become official. If there were any BSM breakthroughs in the data analysis done so far, we'd have heard of it by now.
DeleteThe most interesting physics is the measurement of CP violations in decays of D0 vs bar-D0.
Deletehttps://www.nature.com/articles/d41586-019-00961-w?utm_source=Nature+Briefing&utm_campaign=1e395c7ca2-briefing-dy-20190322&utm_medium=email&utm_term=0_c9dfd39373-1e395c7ca2-43586185
Yes that's in the popular news. has Moriond released new bounds on SUSY such as gluino's and squarks?
Deletegiven Morion hasn't seen SUSY in the full data set, it seems the likelihood of a 5-sigma discovery of SUSY is low.
So far evidence for s-tau or s-top etc is at best around 2-sigma. It has not risen to the eyebrow raising level of 3-sigma. The most recent thing I have seen is
Deletehttps://arxiv.org/abs/1903.07070
Doctor Hossenfelder,
ReplyDeleteIn response 17, having pointed out that you are only one person, the criticism is not relevant because there exists a wealth of ready available alternatives already.
To suggest a few (sorry, just my personal interests): Fusion Energy; Carbon Removal from the Atmosphere; Efficient Storage of Renewable energy sources during times of over-production; higher temperature superconductivity; Neurobiological Research; Cognitive and neurological health; Structures encouraging responsibility and objectivity in leadership.
I don't think diverting (even more) funds from the foundations of physics research into engineering research (and a bit of biology and medical sciences) is the right way to go (and I don't think that's what Sabine proposes, I trust she'll correct me if I misinterpreted her). Those $20 billion should stay in the same field of research, but funding 5-100 promising experiments instead of one mega-project with few to no chances of getting a breakthrough. Or even a different huge project if you have the justification.
DeleteBiology, biomedicine and engineering are already attractive research fields for which funding, private and public, is *relatively* easy to come by. Physics (specially foundations) is extremely hard to sell to the public and the chances of private funding are close to nil. Please, do not advocate for moving funds away from physics, we *need* physics research.
Javier,
DeleteSabine has never seemed to me to suggest diverting funds from physics research. She presents arguments that, in upgrading the LHC, these funds are not being allocated for convincing objectives. Intelligent probing of the unknown, including in the field of theoretical physics, should always be supported. So should building on existing knowledge to directly address massive known problems. Tax supported funding is not unlimited; worthy ideas in all fields die daily for their lack. No single individual can be expected to develop programs which solve all the associated problems. (17.) In suupporting arguments for upgrading the LHC by related developments.in applied science, e.g. in superconducting magnets, the question simply arises whether the known value of advancing applied science should be more directly supported until physics offers programs with a higher probability of definitive results than the LHC. jmo.
Bert Kortegaard
Yes, I'm aware Sabine wasn't suggesting that; you were, though. In my experience, Applied Science is just a fancy way of saying engineering research and, as I said, I don't think we should transfer money from the much-in-need-of-funding foundations of physics into the bad-but-still-not-nearly-as-bad field of engineering research. Superconducting magnets are being actively researched by public and private interests (plenty of direct applications) and although you can always use more funding, they have plenty of opportunities to get it (same with your other proposals). Foundations of physics (QFT, Cosmology, Quantum Gravity, etc) get nearly 0 funding from the private sector because of their lack of immediate applicability and, because of the obscurity of the topics, it's also a hard sell to the public (at the risk of being wrong, I'm guessing they are the worst funded field within the natural sciences; probably only social scientists envy them). That's why while I agree that we should fund something else, I believe the funds should stay in the field. And for full disclosure, I say this precisely from the point of view of someone who does engineering research for a living... in the private sector. Find a theoretical physicist who can say the same (and is still doing fundamental research).
DeleteJavier, thanks for your comments.
DeleteI thought what I was suggesting was obvious from what I wrote, but I apologize to anyone who misinterpreted it as you have.
Applied Science starts where science is understood well enough to build on it to produce useful things. At its most interesting it includes developing new techniques and tools, but ithose of us who practice it do not ordinarily describe that as research.
My blog includes a link to some of my own work in this field.
Lest this should become off-topic, my blog also contains my email.
"...Google make $4 Billion/month from people clicking on their silly little ads. Give science a break......"
ReplyDeleteGod I hope that asinine comment is an attempt at humour..but I have a feeling its not..
On "what novel physical process is going on in the measurement process" I've always assumed it was some sort of Darwinian-like selection-of-fittest-history (in a sum-over-histories formulation of QM). But this process is apparently an additional "postulate" to QM.
ReplyDeleteI love your blog and totally agree that a "wrapping up" of this discussion was due.
ReplyDeleteFor that reason, I would suggest a change in argument 6:
"With it, THESE particle physicists...
"That THE particle physicists MAKING it ..."
Only the ones making the argument suffer from moral corruption. Many others just think it isn't a waste of money, they just have a different opinion (generalization).
It may help avoiding unwanted 'rants'
Ward,
DeleteI think this is clear from the context, but I nevertheless changed that sentence along the line you suggest.
Me as taxypayer I think we should not spend billions of € for a even bigger collider - instead we should invest money in exploring and pondering, where we failed in our beautiful Taka-Tuka-theories during the last half century and consider new ways of thinking aubout the fundamental laws of physics!
ReplyDeleteAs to point 7, maybe NASA's space launch system could use the extra physicists if no new collider is built. They could move from one project with no results to another that is building a rocket that will never launch, because the important thing is to have jobs in all fifty states, not actually get anything done. As Rep. Aderholt said about SLS ""The SLS and Orion programs are, of course, key to the health of our national aerospace supplier base, and it's really helped to really put a new boost of energy into the suppliers in all the 50 states following the retirement of the space shuttle,"
ReplyDeleteBee,
ReplyDeletedo these arguments in these post apply to HE-LHC with 16 tesla magnets, a estimated ~7 billion upgrade to LHC 8.33 tesla magents in its 27 km tunnel?
I would argue that for the price tag, exploring between 14 TEV to 27 TEV for new physics is certainly a justified upgrade.
i wonder whether it'd be better to simply forget about HL-LHC and instead invest that money into HE-LHC.
and by the time 16 tesla magnets are ready, perhaps 24 tesla or even 32 tesla magnets will be in development.
so no new tunnel will be built, the 27 km is reused, but super conducting magnet technology is improved over decades.
"IF" dark matter is made of particles that only interact through gravity, how can you study it if not by missing energy momentum of high energy collisions?
ReplyDelete@Daniel de França MTd2; Dark Matter necessarily gravitates with other matter; it can be studied astronomically; through gravitational lensing and perhaps by studying galaxy dynamics in a wide range of galaxy sizes, or a range of galaxy proximities. What's happening with the dark matter in galactic collisions?
DeleteLet's build a $20B super high resolution space telescope, or 20 $1B telescopes we can gang together in an array. Let's study it.
Dr Castaldo,
DeleteYes but - there's always a but!
The recent paper "Probing dark matter particles at CEPC" by Zuowei Liu and colleagues illustrates the possibility of using high energy colliders to investigate various Dark Matter models.
The point being that thorough investigation of a phenomenon requires multiple lines of attack. This means making the best of the available options - which are often not mutually exclusive. Will collider funding be diverted to astronomy? There's currently no reason to suggest this would be the case.
https://arxiv.org/pdf/1903.12114.pdf
Dr Castaldo
DeleteThis is like studying electrons with circuits. You won't be able to infer what dark matter is, but, just its collective properties. That is, you will just know what a current looks like. You won't get insight of what is dark matter.
Hi Sabine,
ReplyDeleteyou state: The hierarchy problem is not a problem.
Maybe, but if you find a solution you sure will have surprises - surprises that the current foundations may not survive.
Best,
J.
"The measurement postulate"
ReplyDeleteI feel like the justification to question the "Copenhagen interpretation" (you know the one they still teach undergrads) has been around and readily accessible for at least 8 years (https://www.youtube.com/watch?v=dEaecUuEqfc). The problem seems to be that none of the alternative hypotheses (can we call them that?) have been able to gather the doubters together and gain traction.
This business of questioning weather "consciousness" is required for things to be "measured" always seemed daft to me, isn't "superposition" a statement about the correlation or non-correlation of two quantum system not a statement about a single quantum system? ie until I correlate my detector with the superimposed system (by shooting lasers between them I guess would be typical) then the detector isn't 'touching' /hasn't 'touched' the other system and just doesn't contain information about the superimposed system yet? So there is never a funny magic state there is just a situation where two systems don't currently share any information so querying ether of them about the other is nonsensical till you 'connect' the two systems (fire the lasers, take the measurement, open the box, throw the detector at the test article... ect)
Obviously I'm out of my depth please correct my childish simplifications you there smart physical folk! Thank you for the help...
On 17, "you do not know what else to do": I understand you DO know, but --- Since when is knowing the solution to a problem necessary to know that there IS a problem?
ReplyDeleteIf I go to the vet because my dog is limping, I don't go there knowing what should be done about it.
Making it known that a problem exists is the first step, getting agreement on that, and detailing the nature of problem, come next. Developing a plan of attack is well down the list.
It is interesting to me that (re the video link above: The Quantum Conspiracy, 1,571,119 views, GoogleTechTalks) that some physicists like an "interpretation" that says "you don't really exist". It seems to me to be a part of the curious antimaterialist turn (we are all just "information" or something like that) among physicists, at least as indicated by the current articles published for the general reader.
Delete@Philip Thrift, voices that advocate for "antimaterialism" are perhaps more shrill, but for the general reader you could try Philip Ball's "Beyond Weird", https://www.amazon.com/Beyond-Weird/dp/1784706086/, which deflates the weirdness of QM in a way that IMO fairly accurately reflects the practical "let's use QM" perspective of working quantum computing/information, condensed matter, and most working physicists. His Royal Institution lecture, https://www.youtube.com/watch?v=q7v5NtV8v6I, gives a fairly good sense of the position he suggests in that book.
DeleteYou may already know that in philosophy anti-realism is as or more often anti-realism about theories than it is an anti-materialism of anti-realism about the world and our experience of it. There will be some continuity between our current theories and new theories, so that electrons will exist in *some* form in future theories (with careful discussions of how the electron is both equivalent and not quite equivalent to new concepts), but they or other concepts may be deprecated, so to speak, because other theoretical tools and concepts will be devised that are just more effective. An absolute commitment even to such an apparently robust theoretical concept as the electron may, or may not, turn out to be ill-advised, but an appropriate slight hesitancy to say of every part of the standard model of particle physics that it is "emphatically, finally real", does not demand any hesitancy in our belief in and engagement with the world as a whole.
I have read articles about Philip Ball's book (e.g. Peter Woit's https://www.math.columbia.edu/~woit/wordpress/?p=10522), but not the book I admit. My own view has been some combination of Path Integral (or Sum-Over-Histories) and (some version of) Quantum Darwinism: PI+QD. But that's as "real" as I get. :)
DeleteFWIW, the (very popular) idea that the Path Integral (a generating function for time-ordered vacuum expectation functionals) somehow makes quantum theory classical (paths!) is IMO problematic because it uses time ordering to sweep the noncommutative algebraic structure under the table, whereas noncommutative measurements are essential for the empirical success of QM/QFT.
DeleteIf you say "(some version of) QD", I take you to be invoking decoherence in some way, which one has to have formal worries about, but, as you know, it works more-or-less, and certainly for all practical purposes.
My own view has become that QM and QFT are (stochastic) signal analysis formalisms, for which we can say, loosely, that incompatible measurements are mathematical consequences of using classical representations of the Heisenberg algebra, which is closely connected with fourier analysis.
On the PI, I just follow Fay Dowker (@DowkerFay, Mar 26): "This was an enjoyable discussion. I argued that there is one world, not many, in quantum theory based on the Path integral or Feynman sum-over-histories."
Deletehttps://www.youtube.com/watch?v=ZcbXJ7appIE
On "Darwinian" selection: Only one history survives. The others die. Poor things.
Hi , Sabine ��
ReplyDeleteNice discussion.
I agree with you as to a larger collider.
-- I just find it interesting,
the references to 'Tesla'
-- (appearently) without
knowing what it was (is).
-anyway , keep up the good
Work.
-- it is good.
All Love,
re: "Nonsense arguments for building a bigger particle collider that I am tired of hearing (The Ultimate Collection)"
ReplyDeleteBee, the question i have about your arguments in this post is this
CERN has earmarked several billion dollar upgrade for LHC to HL-LHC, to increase its luminosity
is the billions dollars spent to upgrade luminosity by a factor of 2 to 10 a worthwhile use of money?
what about $7 billion more to upgrade LHC to HE-LHC?
HL-LHC and HE-LHC upgrade cost billions, but reuse the same 27km tunnel.
it seems to me if we apply your arguments, we shouldn't bother upgrading the luminosity of LHC, after all, it is still going to CM of 14 TEV, and it seems a 5 sigma discovery at this point is moot.
This was a great thing to read right after opening my bottle of wine :)
ReplyDelete-drl
RE "What should we do?" Martin Harwit wrote a very interesting book in 1981 called "Cosmic Discovery". In it, he shows the amazing role played by serendipity in fundamental discoveries, and tries to get some understanding of how to go forward based on what has led to the current state of knowledge. I think you would enjoy it. This post reminded me of it.
ReplyDelete-drl
What do you think of the latest version of string theory called F-theory?
ReplyDeletehttps://www.scientificamerican.com/article/found-a-quadrillion-ways-for-string-theory-to-make-our-universe/
I think it's a four-letter word they can't say in public
The intense discussion suggests the collider culture has yet to be buried and given up. I have pretty good reasons to believe that we we require new ideas about such experimental research particularly in relation to the ultimate nature of existence and of our realities. It cannot be argued that we have reached the end of all possibilities. However what I have in mind concerns the ultimate nature of forces and particles which if knew would open out a new world of physics.
ReplyDeleteSabine,
ReplyDeleteIt seems to me that several of your arguments boil down to "Cost matters!", contrary to your opponents who are, in effect, arguing "No, Cost does not matter!"
I came close to majoring in economics instead of physics, and I have trouble grasping the mind-set of anyone who truly believe that cost does not matter, but this does seem to be their perspective.
Frankly, I think the subtext of your opponents' arguments is, in essence, "We high-energy physicists are just more important than other people, and doing high-energy physics is just more important than what other people do!" No one will say this quite so bluntly, but I am not sure any of us HEP physicists are completely immune to such hubris. After all, we chose to go into HEP because we really did think it was important.
Of course, scientists should strive for rationality and objectivity, but, obviously, we too are all-too-human!
All the best,
Dave
Dave,
DeleteI am not sure if they actually believe that cost does not matter or whether they just argue this way because they know it's their only chance. Either way, though, what surprises me is that they would even make such an argument, if not explicitly, then implicitly by refusing to explain why the expenses are justified.
Well, yes, everyone thinks that their occupation is the most important. I don't blame anyone for that. But most people understand at least that others might not share that impression.
I find it extraordinary that fundamental physics is now utterly divorced from the rest of science, or anything that matters more widely.
DeleteHEP doesn't seem at all likely to discover a foundational truth - but it is always possible to throw yet more money at it to achieve higher energy collisions, and maybe some more 'particles'. That process will only stop when more people like Sabine put their feet down!
Hi Sabine.
ReplyDeletesome of the latest tests
give credence to your argument.
( high intensity laser / mirror
trap) ...(nano particles)
,.. money can be better spent,
on smaller scales.
--. All Love,
Every ten years the space astronomers get together with NASA and create a new list of prioritized space missions. There is never enough money to fund everything and as science changes priorities change and as technology changes capabilities change. It's sort of what Erdos used to do with mathematical problems, He'd assign a cash bounty, higher for the problems he thought would be most fruitful. The problem with particle physics is that the price is getting so high, even in comparison with the costs of space missions, that funding even one item is just too expensive. No one has been thinking about a Plan B, C or D.
ReplyDeleteMy guess is that we'll start seeing the real spinoffs from the LHC when physicists start leaving the field.
Ms Hossenfelder,
ReplyDeleteI personally think your position against the larger particle collider is very relevant. But I don't think that your arguments can change anything, and that is why : the larger collider has become a collective narrative of the particle physics community. Specialists call that "Intersubjective narratives", those are the root of our human society and when they have got some traction there is no way to kill them by questioning their soundness. By the way most of them are not built on RATIONAL arguments. Think for example of the moon race in the 1960. There was no rational to make such a costly programm without any other purpose than self proudness, but it became an intersubjective narrative of american people and as so impossible to cancel... until the mission succeeded and we could see there wasn't anything usefull to get from it. Il you do want to prevent that project there are in my view only two ways :
1/ leave the scientists and go to the politicians who will ultimately give the money.They most probably are not in the narrative of the particle physics community and could listen to the voice of the reason. But don't expect that the money not spent on the super collider will go in any massive way elsewhere in physics ;
2/ build another narrative on another subject and try to give it traction. To do that you have to get massive support within the physics community not just on criticizing the new collider idea but more importantly on one and only one other project which could get most of the money that could go to the collider.
That does not seem fair to all the other good ideas which could benefit of a funding ? Yes, but life is not fair.
Franck,
DeleteI think what you mean by "rational" is really "scientific". I agree that there are reasons besides the scientific ones that make people spend money on large science projects. I have nothing to say about those, so I don't. But I wouldn't call them irrational.
You seem to be misunderstanding my intention though. I am not writing to prevent something from happening. I hope to make something happen. I hope that physicists who work in the foundations think about what has gone wrong and how to make progress. Blindly throwing money at the problem will not solve it.
You seem to expect me personally to come up with a solution and then convince people to support me. This does not make any sense. Of course I have my own convictions about what is the right thing to do, but I don't think I should be the one making decisions. I merely want physicists to use their brain rather than blindly continuing down dead end streets.
It's not about fairness, it's about progress.
Franck; Sputnik was launched in October, 1957. To Americans, it was widely considered a dire threat.
DeleteRussia then put the first man in space four years later. Kennedy needed a response to a potential militarization of space; there was a perceived necessity to not let Russia seize "the high ground".
Kennedy considered a number of potential operations, but "putting a man on the moon" before Russia did seemed the most likely to succeed, with the most inspirational content to get public backing.
There were very rational ideas behind this program, even if the ultimate goal was just a symbolic finish line. The point was to develop the science and technology and capabilities of the space age, to match the same being developed by a hostile power (the Cold War was 14 years old at this time), and this is what was accomplished.
There were many entirely rational reasons to "go to the moon", including the rational decision to appeal to emotions in building public support.
Because, as we Americans are currently proving, and other countries have proven time and again throughout recorded history, rationality is definitely not the primary decision making tool of our citizens.
@Franck: That "life is not fair" is not an excuse for taking action to make life more unfair; the primary value of human intelligence has surely been to make us far less victims of the random cruelties of life and nature, not to exacerbate them.
DeleteThe solution to one swindle is not another swindle, it is getting people to recognize when they are being swindled.
With respect to the discussions on the foundations of quantum mechanics and measurement I write this below.
ReplyDeleteProbability theory for statistically independent events is L^1 in that probabilities add linearly and there are no correlations between probabilities. Quantum mechanics is L^2 in that amplitudes add linearly, but the “distance,” or really most importantly the distance squared as probabilities, is the sum of the modulus square of amplitudes. This makes statistical mechanics or a theory based on pure classical probability fundamentally different from quantum mechanics.
The theory of convex sets is such that for a set with measure L^p, with elements x, and another with L^q, with elements y, that Holder's norm ||x||_p×||y||_q ≥ sum_i|x_iy_i| for 1/p + 1/q = 1. This means there is a duality between convex sets with these values of p and q defining these norms. For p = 1 this means q → ∞ and for p = 2 the dual is also q = 2. This is a part of how quantum mechanics and spacetime, with its Gaussian metric distance, are dual to each other. The dual to pure statistical systems with q → ∞ means there are no probabilities at all and this is a completely deterministic system such as Newtonian mechanics.
A measurement occurs where there is a decoherence of a quantum wave occurs and the trace elements of the density matrix defines a classical probability distribution. The theory of decoherence permits us to understand how a wave function is reduced, because the superposition or entanglement phase of that system is transferred to a reservoir of states, say the needle state of a measuring apparatus, and the system is reduced to pure probabilities. We can't really know which of these outcomes happens in some deterministic manner according to quantum mechanics.
As the dual for a p = 1 system, where the wave function reduction is a p = 2 → 1 process, has as its dual the q → ∞ convex set or hull description. Does this then mean we can use this to understand some underlying classical type of structure to quantum measurement? We might want to be a bit conservative here. The problem is that we have convex sets that we propose are computing quantum numbers, and in the case with a p ↔ q duality we have this idea that quantum numbers, say as the Gödel number for an integer computed by a Diophantine equation or the computed outcome of a deterministic system, as having a single axomatic process. Hilbert's 10th problem proposed there should be a single algorithmic or axiomatic process for solving Diophantine equations Matiyasevich found the final conclusion to a series of lemmas and theorems worked by Davis, Putnam and Robinson, called the DMPR theorem. This is a form of Gödel's theorem and the conclusion is there is no comprehensive axiomatic system for Diophantine equations. Quantum numbers as Gödel numbers for integer solutions to Diophantine equations are then not entirely computable and there can't exist a Turing machine (in the classical sense a q → ∞ convex set) that computes quantum outcomes.
I then maintain the solution to the quantum measurement problem is that there can't exist such a solution. It is an unsolvable problem. Quantum measurement has some features similar to self-reference in that a quantum system is encoded by another system ultimately made of quantum states. It also has features similar to the Euclid's 5th axiom problem. One can assume the axiom holds and stick with Euclidean flat space, or one can abandon it and work with a plethora of geometries. In QM this would be to stay with Merman’s shut up and calculate dictum, or to adopt any of the quantum interpretations out there, which contradict each other, to augment QM in some extended way. This has features remarkably similar to the dichotomy between consistency and completeness.
@LawrenceCrowell, this is fine, but I suggest there is a question as to what Classical Mechanics is. Specifically, Koopman in 1931 introduced a Hilbert space formalism for CM, which can be thought of as offering a unification of CM with QM, just as the Schrödinger equation and Heisenberg's matrices were unified as Hilbert space formalisms. In these terms, the difference between CM and QM is mostly "just" that CM has a purely commutative algebra of measurements. Mutually noncommutative measurements do make sense for CM, however, as is well-known in signal analysis, where Wigner functions are frequently used: one can introduce the Heisenberg group as differential operators, [j∂/∂q,q]=j, instead of as in QM as [q,p]=i. Call an extension to include all such operators CM+. I lay out an argument that if we have a solution of the measurement problem for CM+ (using a Gibbs state over the CM algebra extended to the CM+ algebra), we also have a solution for QM, in my https://arxiv.org/abs/1901.00526 (currently submitted to Physica Scripta): I find that a solution for CM+ is less elusive. In particular, I suggest that the specific difficulty you outline above is eliminated by comparing CM+ with QM instead of comparing CM with QM. We don't obtain a complete unification, but it's closer than we've had.
DeleteI looked over your paper and down loaded it. I will have to reserve judgment until I read it sometime later, though I hope not too long into the future. It looks a bit like noncommutative geometry of Connes et al..
DeleteThe connection between quantum and classical mechanics is often stated as 1 = {q, p} → [q, p] = iħ for large action S = nħ for n → ∞. I think the most important aspect of this is that classical mechanics is real valued and quantum mechanics is complex valued. The extension of the reals into complex numbers means probabilities are the modulus square for |ψ⟩ = sum_n c_n|n⟩
⟨ψ|ψ⟩ = sum_{mn}c^*_mc_n⟨m|n⟩ = sum_n|c_n|^2 = sum_n P_n.
Classical mechanics has none of this construction, and instead determines the value of classical variables. The correspondence between an observable Ô|n⟩ = O_n|n⟩ in quantum mechanics and probabilities is then
⟨ ψ| Ô |ψ⟩ = sum_{mn}c^*_mc_n⟨ m| Ô |n> = sum_n|c_n|^2 = sum_n P_nO_n.
This is Born's rule, where curiously a general proof of this is not at hand. Anyway the observable occurs as eigenvalues in a distribution with probabilities. We can think of both classical and quantum mechanics as a measure theory O_{obs} = ∫dμO, but where for classical mechanics the measure is zero everywhere except the contact manifold and the with quantum mechanics there is this quadratic set of modulus square of amplitudes = probabilities in a summation that weights eigenvalues.
There is Gleason's theorem that tells us the linear span of a Hilbert space defines a trace that uniquely defines probabilities. Hence any measure μ(X) = Tr(WP_X) for W a positive trace class. So this appears half way to a complete proof of Born's rule; all we need is to slip operators in this. The problem is that operators come in sets of commuting operators. In particular the density matrix evolves by ρ(t' - t) = Uρ(t)U^† for U = exp{-iH(t' - t)/ħ}. For t' - t = δt very small then U ≈ 1 - iH(t' - t)/ħ and it is not hard to see that time evolution of the density matrix involves a nonzero commutator of the density matrix with the Hamiltonian. This means the Hamiltonian rotates or evolves the density matrix out of the basis one might consider for Gleason's theorem. I think this is the reason that Gleason's theorem, as profound it may be, does not reach the generalization of a proof of Born's rule.
However, observables in classical and quantum mechanics have different measure theories or distributions. Classical mechanics is “sharp,” which means it it L^∞ --- say like a delta function. Classical mechanics is L^2, and the metric structure of spacetime is L^2 as well and with conformal spacetimes and R_{ab} = κg_{ab} it is also L^2. Without getting further this is a duality connected with building spacetimes with entanglements. Now with 1/p + 1/q = 1 for convex sets then L^∞ is dual to L^1, which is a measure of pure classical probabilities. So what is this system? It is about complete stochasticity, which the outcomes of measurements are an example of. The question is whether the eigenvalues of the QM L^2 coded as integer solutions to Diophantine equations, something proven to be possible by Matiyasevich as any function has a corresponding Diophantine equation (even transcendentals like e^{ix} etc).
LC
Not so much Connes as an algebraic QM approach, with the intention to bring it down to a mortal (my) mathematical level (I'm just reading Valter Moretti, "Spectral Theory and Quantum Mechanics", Springer, 2017, for example, where his Chapter 14, "Introduction to the Algebraic Formulation of Quantum Theories, is nicely done).
DeleteThe starting point for both classical (as usually understood, a commutative *-algebra) and quantum (a noncommutative *-algebra), as I take it, is that a state over a *-algebra is a normalized, positive map to average measurement results.
The GNS-construction gives us a Hilbert space in both cases. Normal states are given by Trace[Aρ] in both cases and the Born rule is "just" a measurement |ψ⟩⟨ψ| in a pure state with density matrix ρ=|φ⟩⟨φ|,
Trace[|ψ⟩⟨ψ|φ⟩⟨φ|]=⟨ψ|φ⟩⟨φ|ψ⟩=|⟨φ|ψ⟩|².
Note that everything is linear until we insist on discussing pure states.
The key question is to ask whether classical physicists can reasonably ascribe a meaning to all operators that act on the classical Hilbert space, to which I argue that they can. Transformations to a different basis, with the fourier transform as case in point, more than just making sense, are *used* in classical signal analysis.
I'm doing very little that's specially new in this QM context. As I said, Koopman suggested such an approach in 1931; von Neumann wrote a long paper in German that has *not* been translated, so of course it's called the Koopman-von Neumann approach, but the approach mostly languished until about 2000, when a PhD thesis appeared, since when there has been a slow stream of papers, and for the last few years there has been a Wikipedia page that's not bad. Recently a connection has been made with Quantum Non-Demolition measurements, which seems to have led to slightly more interest. I believe that understanding how things look in this kind of approach deserves to be at least as much in physicists' consciousness as deBB approaches.
One final comment: *I* take the view that the complex structure *can* be understood rather nicely as associated with the fourier sine and cosine transforms of probability densities, which, as any engineer can tell you, introduces a naturally useful imaginary, j. I'm not committed to that approach, but so far I haven't seen a more natural approach.
I ought to let the paper do its own talking, given that you've kind enough to say that you have at least downloaded it, but I'm quite keen to see in what ways it might or might not be attractive to other people.
The GNS construction is an aspect of noncommutative geometry. The spectra with Tr(Aρ) is also used in Gleason's theorem.
DeleteI will try to get to your paper as soon as possible. I have this large backdrop of things to read, including finishing Sabine's book. I started reading a library copy last year and have since bought my own copy and that is on my stack as well.
This comment has been removed by the author.
ReplyDeleteIn The EU, Canada and 'Developed Asia' , the budgets for Science and technology seems to not be at Risk ... It is U.S.A. that prioritize their Budgets in Military Applications the ones that knows that They have to make their research agendas to fit into Geo-Political Military Conflicts to get The Money ... (ROFL) ...
ReplyDeleteVery Likely, The EU's headquarter are waiting to China's Parliament approve their Budget for HEP projects ... after that, They will decide ...
No Problem, Some CERN physicists will be invited to participate in China's Toys ... and CERN will receive its 'upgrading' budget ...
There is not an Eternal HEP Vacuum in Your Future ...
Don't Cry in advance for things that are not happening ...
@Sabine,
ReplyDeleteI do not quite see what this "measurement problem" is, although apparently some people lose sleep over it. The view of standard QM+ decoherence is perfectly reasonable:
Schroedinger's equation (SE) describes a closed quantum system. But when the system is measured, it cannot be considered closed anymore, so it is no surprise that it's not described by the SE. The collapse of the wave function is just an effective prescription that describes this coupling to the external environment induced by the measurement. Decoherence theory showed how this process can be explained in detail in terms of standard QM. So really, I do not see where is the problem.
From the experimental point of view, the experiments of Serge Haroche, for instance, have clearly shown that when the "environment" is sufficiently simple, the decoherence can be well controlled or even reversed. Again, no mystery there.
I would not spend gigadollars, not even megadollars, on this pseudo-problem. For K$, I'm OK.
Opamanfred,
DeleteDecoherence does not solve the measurement problem. Please do some reading. Don't worry, I do not want your "giga-dollars".
The following video simulates the collapse of the wave function. This gives pretty good ideas of how probability plays a role in collapse and what visually a collapsed wave function appears as. Of course a caveat is in order, for the ontology of a quantum wave is highly uncertain and it does not exactly "appear." However, this tells us about the mathematical representation. This video also makes the point that this sudden transition is not something the Schödinger equation predicts.
Deletehttps://www.youtube.com/watch?v=p7bzE1E5PMY
As I wrote above dated 3/31 I think very strongly this problem is not solvable. Of course I might be wrong, but the issue of quantum measurement appears remarkably similar to the concept of self-reference. Instead of a predicate acting on Gödel numbers for predicates including itself a measurement is quantum information encoding quantum information.
Decoherence does address aspects of measurement. However, it does not tell us how a particular outcome occurs, but rather how probability amplitudes transform into classical-like probabilities as quantum phase of superposition or entanglement is transferred to a reservoir of states. Decoherence takes us right to the doorstep of the measurement dragon, but no further.
"Decoherence does not solve the measurement problem"
DeletePlease elaborate. I would also like to hear how exactly you define the problem. I consider what I sketched as a perfectly acceptable solution. On what aspect do you disagree?
Opamanfred,
DeleteThis is really off-topic. I am one person and not a forum. I do not have time to respond to random questions. Really, this is common knowledge, and in any case, I explained this in my book, and also Lawrence explained it correctly when he writes:
"Decoherence does address aspects of measurement. However, it does not tell us how a particular outcome occurs, but rather how probability amplitudes transform into classical-like probabilities as quantum phase of superposition or entanglement is transferred to a reservoir of states."
Lawrence,
DeleteRe the measurement problem:
...I think very strongly this problem is not solvable.
Well, it is not solvable mathematically speaking because it is not a question of mathematics, but of physics. The question involves the nature of the physical processes underlying the maths of QM.
The difficulty, of course, is that those processes are not directly observable, and the standard formalism does not resolve logically to a realistic picture of the quantum subsystems - a wavefunction is not a physical thing.
The resulting ontological speculations (MW,PI, superposition) based on the maths are muddied, metaphysical, and lacking in scientific significance, to say the least. The Copenhagen approach, OTOH, is simply to ignore the ontological problem, which consequently induces the measurement problem.
Only Bohmian mechanics approaches the ontological problem from a physics (rather than strictly maths) perspective by assuming that quantum subsystems are ontologically continuous with classical mechanics. That this physically realistic reformulation (of QM) is currently disfavored relative to all the logically strained, metaphysical interpretations (of QM), says nothing good about the state of modern theoretical physics.
BM is mathematically equivalent (but not qualitatively identical) to QM. In Bohmian mechanics there is no measurement problem. So, problem solved, no?
I have certain proclivities for the Bohm interpretation. I suppose this is just as I have the same for other interpretations. In fact I derived a form of path integral with Bohm's quantum mechanics. I found the mention of Bohm was a form of toxin in getting this published. Bohm's QM is also potentially interesting for solving problems in chaos or quantum chaos. Bohm's QM is though not identical to QM in general, but only so for wave functions of a certain form. Bohm's QM has some other deeper problems as well.
DeleteThe Klein-Gordon equation is a scalar wave form of the invariant momentum-energy interval of special relativity. If you follow the Bohmian prescription with a polar wave function you find the KG equation has the quantum potential. The odd implication is that a massless particle is off the light cone and in fact moving faster than light. This does not give reason to think there are various nonlocal physics with this, for that violates no-signaling and other things. This is why it is often said that Bohm's QM is not relativistic. Bohm's QM also without a Hilbert space does not derive things such as the generation or absorption of photons by atoms in a concise way, and things get worse with higher energy creation and annihilation of particles.
There are quantum interpretations that are ψ-epistemic and other that are ψ-ontic. The many world interpretation (MWI) and Bohm interpretation (BI) are ψ-ontic. Bohr's Copenhagen interpretation (CI) and now the latest Qubism by Fuchs are ψ-epistemic. These are some of the popular interpretations and there are others such as consistent histories, the Montevideo interpretation and the related one by Penrose, and other. In fact quantum interpretations are multiplying like bunnies, maybe cockroaches to put it in a negative light, and none of them seems to really solve everything. The CI is interesting in that M-theory of D-branes works well with it. Quantum information theory is worked often in MWI. Qubism is now the beautiful child of those into Bayesianism --- which I can tip my hat towards. Pullen and Penrose have interesting ideas on how gravitation plays a role, and quantum gravitation built up from quantum entanglements probably does have a correspondence with quantum wave decoherence and maybe even measurements. However, all of these have big holes you can run an optics bench through, maybe even a collider.
I wrote a math-physics result on how quantum mechanics is neither ψ-epistemic or ψ-ontic with any certainty. It does not work for two state systems, which is unfortunate. I should revisit this to make it work. The result is that quantum interpretations that are either ψ-epistemic or ψ-ontic are not determined by a measure theory of QM. I like the prospect of this: QM has this sort of Man proposes and QM disposes flavor to it.
@Lawrence Crowell
DeleteLast Spring I submitted a short essay to the Gravity Research Foundation (GRF) in Wellesley, Massachusetts, that effectively is another interpretation of QM; albeit, a very amateur one. The concept is largely heuristic with a minimum of mathematical modeling. Currently I'm expanding on the original paper, submitted to the GRF, to include ideas for which the essay word limit (1500 words) would not allow. In the abstract of the paper, submitted to GRF last year, a tie-in to De Broglie-Bohm Pilot Wave Theory (PWT) is mentioned. This might have been a mistake seeing that PWT is anathema to much of the physics community as illustrated by your choice of the word "toxin", to describe the reaction of publishers to that particular QM interpretation.
While I didn't mention it directly in the essay submitted to GRF the model provides a mechanism for reported anomalous acceleration signals observed in certain superconductor experiments that are orders of magnitude larger than allowed by standard physics (Tajmar et. al. 2003-2006, and others). This connection provided the rationale for submitting the essay to GRF, as the organization's stated mission involves understanding gravity, and presumably artificially generated gravity-like forces. To wind this up, I hope to complete the expanded version of the originally submitted GRF essay in a few weeks and upload it to viXra.org.
The particle in the pilot wave interpretation of Bohm and taken from deBroglie is not highly regarded in part because of Bohm's intention with local hidden variables. The idea is workable in a nonrelativistic framework and I think a way of working quantum chaos.
DeleteThere is a fascinating way of doing quantum mechanics that Pascual Jordan worked with Wigner. It is a way of doing QM with trace and determinants that is useful with the Freudenthal determinant over exceptional algebras. In fact I think it is useful with permanents as well, which find their way into algebraic geometric complexity and P vs NP. So why is this not widely used? Jordan and Wigner published on this in 1935 and Jordan became fanatically committed to the Nazi cause. He worked on the rocket programs at Peenemunde and was committed to the Nazi program. It is amazing how this sort of crap can infect brains, much like MAGA promoted in the US these days. Anyway this approach to QM fell into disrepute. History and affiliation have big impacts on the course of development in physics.
This comment has been removed by the author.
DeleteIn fact quantum interpretations are multiplying like bunnies, maybe cockroaches to put it in a negative light, and none of them seems to really solve everything.
DeleteWell yes, but the Bohmian advantage over all those proliferating bunnies is twofold. First, it eliminates the self-induced measurement problem of CI. More importantly, it provides a qualitative account of unobservable quantum processes that is continuous with classical mechanics and therefore provides a sound (and realistic) basis for further qualitative and quantitative elaboration.
The continuity with CM is achieved by introducing a scale factor, the guiding equation. This guiding equation, in turn, is suggestive of an underlying physical component that induces quantum behavior in sufficiently low-mass classical particles.
This avenue would seem to offer, at least the possibility, of a qualitative and quantitative approach with the potential to converge on a plausibly realistic account of quantum phenomena. I don't think the same can be said for any of the other cockroaches.
Okay, okay. But what if we find more Odderons? ;)
ReplyDeleteThis conjecture on my part is not something I have actually bent metal on or have done any calculations. This is pretty removed from my day job work that is more applied or engineering. The DMPR theorem is similar to the Bernays-Cohen result that the continuum hypothesis is a case of Gödel's theorem.
ReplyDeletePolytopes also enter into the algebraic geometry complexity of N vs NP. The role symmetry is of course important for gauge fields. Also for quantum entanglements quotient spaces or groups occur when some set of quantum numbers are replaced by other degrees of freedom. A bipartite entanglement replaces the spin of two fermions with the Bell state. This is a quotient system. The exact sequence for the moduli space of gauge connections is similar. In fact I think dual to entanglement geometry.
I often wonder what a theory will look like that explains QM and ART as special cases. As far as I can see, most scientists are trying to bridge the gap from QM. This seems logical, since most physicists probably regard QM as the most fundamental theory. However, the classic cases of really new theories have developed differently. There was no direct path from classical physics to quantum mechanics, nor to GRT. So QM and GRT were really new. Therefore, the question is whether the current approaches to unifying the two basic theories can really be promising enough.
ReplyDeleteI myself am a mathematician with a solid background in Artificial Intelligence.
When developing an algorithm for decision-making, I came across interesting relationships rather playfully. The chaotic decision process (I call it the "GenI process") is a chaotic random process based on very simple rules. Except for the basic arithmetic in complex number space, this does not require any difficult mathematics. (Simple maths do not necessarily produce simple results: think of the fractal sets by Mandelbrot.)
Significantly more difficult is the statistical analysis of chaotic state changes. On the one hand, I can show that the process, starting from an initial state, certainly selects one of several decisions, and thereby exactly fulfills the statistics known from quantum mechanical measurements. On the other hand, I can derive a relativistic metric such that averaged state changes follow time-like geodesic paths in a four-dimensional Riemann space.
Should not such or similar approaches, which are not derived directly from QM or GRT, ensure a fresh start? In principle, this is only about a change of perspective.
@WSG
ReplyDeleteThere is a upcoming version of QM that uses complex numbers and four-dimensional Riemann space. It's used to handle open systems.
It is called PT-symmetric quantum mechanics.
PT-symmetric quantum mechanics is an extension of conventional quantum mechanics into the complex domain. (PT symmetry is not in conflict with conventional quantum theory but is merely a complex generalization of it.) PT-symmetric quantum mechanics was originally considered to be an interesting mathematical discovery but with little or no hope of practical application, but beginning in 2007 it became a hot area of experimental physics.
http://www.europhysicsnews.org/articles/epn/pdf/2016/02/epn2016472p17.pdf
This is not the point I wanted to make. This is obviously just another extension of a proven theory. Such things did not lead to anything really new. I am well aware of other approaches, such as quantum loop gravity or string theory, which, despite all efforts, have yet to resolve the open questions.
ReplyDeleteThe question of what a theory must look like so that QM and GRT can be deduced from it have already been asked. Maybe it will look somewhat crazy from today's perspective, as the QM for classical physicists.
My point is to take a fundamentally different perspective on the role of gravity in QM.
A model like the one mentioned above indeed requires a rethink. After that, our universe, as we perceive it, evolves according to a collapse of its wave function. This clearly contradicts the not explicitly justified assumption of leading physicists that it develops along a Schrödinger equation. But why is it like that? Is there a clear justification and vice versa? What, in essence, is against assuming a collapse? I have not even seen a discussion among physicists about this aspect. Even with well-known authors like Penrose, Greene, Hawking, who otherwise like to talk about the wildest speculation, nowhere is there any hint that the collapse of its wave function is the source of reality in our universe.
Can anyone help me here? Are there any works that consider this perspective?
At least in a nutshell, I can prove that such an approach can be quite effective. I can perform concrete calculations of a space-time metric for a spin1 / 2 particle and actually prove that the dynamics during the measurement satisfy Einstein's field equations. That should justify at least a discussion about the view.
Thank you for this exceptionally thoughtful post. I do think that a good question to ask people on both sides of the argument is: What is your cutoff?
ReplyDeleteThat is: For supporters of the collider, I'd like to ask "How expensive would this thing have to be before you stopped supporting it? 30 billion? 50 billion? 100 billion?"
And for opponents: "How inexpensive would this thing have to be before you stopped opposing it? 15 billion? 10 billion? 1 billion?"
As a general rule, I think people who are able to answer these questions --- and to defend their answers --- are likely to have thought a lot harder about the tradeoffs than those who reflexively just support or oppose.
Steven,
DeleteYes, a good question. I'll make a go at it and say about $2 billion.
Reason:
A larger collider currently has less scientific promise than LIGO had, which came in at a cost somewhat below $1 billion. It has also less scientific promise than the SKA, whose full proposal would come in at $2 billion. So that would seem a reasonable amount.