Sabine Hossenfelder and Beauty in Physics

[jedishrfu]

From the article:

Who doesn’t like a pretty idea? Physicists certainly do. In the foundations of physics, it has become accepted practice to prefer hypotheses that are aesthetically pleasing. Physicists believe that their motivations don’t matter because hypotheses, after all, must be tested. But most of their beautiful ideas are hard or impossible to test. And whenever an experiment comes back empty-handed, physicists can amend their theories to accommodate the null results.

This has been going on for about 40 years. In these 40 years, aesthetic arguments have flourished into research programmes—such as supersymmetry, the multiverse and grand unification—that now occupy thousands of scientists. In these 40 years, society spent billions of dollars on experiments that found no evidence to support the beautiful ideas. And in these 40 years, there has not been a major breakthrough in the foundations of physics.

https://motherboard.vice.com/en_us/...ists-are-misled-by-outdated-notions-of-beauty

 

[Dr. Courtney]

Picking which theory is right is always a matter for experiment.

Picking which theory is more worthy to try an experiment on is not an endeavor that science has provided a clear path on.

The culture of science has evolved from highly capitalist in the 16th-19th centuries (whoever could pay for it did the experiments they wanted to do) to highly socialist in the 20th-21st centuries (the expense and scale of much science leads to an elite deciding how to spend government money on which ideas to develop and test.)

We simply do not have a clear set of principles to know how to develop theories how to pick more promising theories before the experiments are done. Beauty in a theory is no more an objective criteria than beauty in a woman or a building or a landscape. Simplicity is similarly challenging to define objectively.

Nice article, thanks for posting the link.

 

[romsofia]

I think a good article to read if you haven't already is: https://arxiv.org/pdf/1710.07663.pdf

Especially the section on "The role of theory":
“The truth is, the Science of Nature has been already too long made only a work of the Brain and the Fancy: It is now high time that it should return to the plainness and soundness of Observations on material and obvious things.” These words are not the latest attack against the abstractness of modern theoretical physics or the inability of string theory to find a criterion for empirical falsifiability. No, these words are by Robert Hooke and date 1665 [52], when times were changing in England and a new approach to science was emerging: a radically different use of abstract mathematics in formulating physical theories. Only one year later, in the annus mirabilis 1666, Isaac Newton, who had no sympathy for Hooke – sincerely reciprocated by Hooke – started to revolutionise physics by making use of calculus in his formulation of mechanics and gravitation. A masterpiece of a work of the Brain."

But some things on the article in OP:

I honestly don't like the approach in the article in OP. It seems foolish to me to assume that people are looking for "beauty" and the author seems to be coming at the issue with a whole bunch of hindsight. The one quote I dislike the most is: "My conclusion from this long line of null results is that when physics tries to rectify a perceived lack of beauty, we waste time on problems that aren’t really problems."

Throughout history, people take the wrong roads, but if you never allow them to take the road, how do you know it's wrong? Only through hindsight can the author state that they aren't "really problems".

I do research in QG, and I dislike where the field is going as well. We haven't found SUSY, but they keep changing their goals in order to protect the idea behind it. But there is logic behind it all. They take the quantum fields to be very fundamental because the logic behind that formalism has been so accurate in experiments. So the "beauty" behind them IS WORKING, so it isn't foolish to think that logic would keep working.

I'm not sure what particular approach Sabine Hossenfelder takes to solving the quantum gravity problem, but I think it's ignorant to say that supersymmetry isn't a "real problem".

 

[Dr. Courtney]

Throughout history, people take the wrong roads, but if you never allow them to take the road, how do you know it's wrong? Only through hindsight can the author state that they aren't "really problems".

Do you really mean allow? Or do you mean "pay for"? I've never heard a suggestion that a scientist in the US or west would not be allowed to pursue any idea as long as they arranged their own funding. Usually, the complaint is closer to demanding money for the pursuits from the government treasury - money taken from the taxpayer at threat of legal action.

 

[stevendaryl]

I'm not sure whether I agree with her about this. It is true that all the various elegant and beautiful approaches to go beyond the standard model (string theory, supersymmetry, loop quantum gravity, Grand Unified Theories) have not produced anything much. But is it because the researchers were driven by the desire for beauty? It seems to me that the successes of foundational physics were also driven by similar desires to unify and streamline our laws of physics. Combining the laws of magnetism and electrical forces into a single topic of electromagnetism was the sort of unification activity that seems to have fizzled out recently. So was General Relativity. So was quark theory and QCD. Her point might be that these efforts were guided by experimental results, so there was a twin motivation, aesthetic and experimental. I would not say, though, that the experimental motivation was the only thing. In GR for instance, Einstein's motivation was to unify SR and gravity theory. It was a matter of pursuing coherence, rather than addressing experimental puzzles (there certainly were empirical consequences to GR, but they were not what motivated Einstein).

The real reason, in my opinion, that work in foundational physics has slowed recently is basically because of the lack of ideas for experimental evidence that goes beyond the predictions of the standard model. In some sense, as ugly as it is in some ways, the standard model is just too good. It agrees too well with experiment. You need experimental puzzles to solve to advance science.

Now, I do think that cosmology, as opposed to particle physics, does have a lot of observational puzzles to solve. But unless the solution connects with something experimental (which I think of as different from observational, in the sense that in an experiment, you can choose the setup, while in observations you have to take what the universe gives you), it's hard to see how a theory can go beyond the "guessing" stage.

 

[Dr. Courtney]

The real reason, in my opinion, that work in foundational physics has slowed recently is basically because of the lack of ideas for experimental evidence that goes beyond the predictions of the standard model. In some sense, as ugly as it is in some ways, the standard model is just too good. It agrees too well with experiment. You need experimental puzzles to solve to advance science.

Now, I do think that cosmology, as opposed to particle physics, does have a lot of observational puzzles to solve. But unless the solution connects with something experimental (which I think of as different from observational, in the sense that in an experiment, you can choose the setup, while in observations you have to take what the universe gives you), it's hard to see how a theory can go beyond the "guessing" stage.

You have some very nice insights there. Thanks for sharing. Great contribution.

I wonder how absolutely you mean the following statements:

You need experimental puzzles to solve to advance science.

Do you mean that new experimental puzzles are an absolutely firm requirement (science cannot possibly advance without them)? Or do you mean that advancing science will be much harder and take much longer without them?

But unless the solution connects with something experimental (which I think of as different from observational, in the sense that in an experiment, you can choose the setup, while in observations you have to take what the universe gives you), it's hard to see how a theory can go beyond the "guessing" stage.

I think I get your meaning, but clarification would be helpful. My view (and experience) is that eventually observation will provide what is needed for the testing of new theories/hypotheses but it may take lots longer and require greater patience and possibly expense. If one waits long enough and is clever enough, eventually the universe will give what is needed through observation to test many theories. In many ways the observation of black holes colliding provided an onservational test of GR in ways where it is hard (at least for me) to conceive of an experimental test. But the observational approach required building a sensitive detector and waiting.

 

[Vanadium 50]

This has been going on for about 40 years. In these 40 years, aesthetic arguments have flourished into research programmes—such as supersymmetry, the multiverse and grand unification—that now occupy thousands of scientists. In these 40 years, society spent billions of dollars on experiments that found no evidence to support the beautiful ideas.

Counter-example: the Higgs mechanism.

 

[Vanadium 50]

If Hossenfelder would then turn around and argue "But it's been 6 years since the Higgs", I might then turn around and point out that in those years, she published 11 papers with a maximum of 14 citations, while the LHC experiments have published 1000 papers with a maximum of 1000 citations for non-Higgs results. If I were feeling uncharitable, I might even question whether she has correctly identified who has a lack of progress.

 

[anorlunda]

My view (and experience) is that eventually observation will provide what is needed for the testing of new theories/hypotheses but it may take lots longer and require greater patience and possibly expense. If one waits long enough and is clever enough, eventually the universe will give what is needed through observation to test many theories.

In my view, that much optimism is too much.

For example, I suspect that we will never be able to resolve which QM interpretation is correct, or what happened before the "origin" of the universe, Yet we have many scientists studying those things as a career. I just met a post doc at Dartmouth who is planning on spending the rest of his life on MWI. My reaction was, "What a waste of taxpayer money. He will likely never contribute anything to the state of the art in an entire lifetime."

I recognize that you said, "If one waits long enough" and that is unbounded. In the future, we will have better methods and better tools and there is no defined upper limit to "better." But those might come from advancements in other areas like electronics, rather than from MWI scientists. Therefore the prudent policy would be to table some of those science investigations for several centuries until technology makes it possible to succeed.

I say the same thing to people on the engineering side who insist that technology will inevitably produce FTL travel given sufficient advancements.

.

 

[stevendaryl]

For example, I suspect that we will never be able to resolve which QM interpretation is correct, or what happened before the "origin" of the universe, Yet we have many scientists studying those things as a career. I just met a post doc at Dartmouth who is planning on spending the rest of his life on MWI. My reaction was, "What a waste of taxpayer money. He will likely never contribute anything to the state of the art in an entire lifetime."

I might agree that research on quantum interpretations or MWI is unlikely to produce anything. However, that research is certainly not a significant waste of research dollars. Theorizing at your desk is a LOT cheaper than building huge experiments. LHC, for instance, cost $13.25 billion to build, and then there's operating costs, computing costs to interpret the data, etc.

 

[PeterDonis]

Counter-example: the Higgs mechanism.

That was just a confirmation of the Standard Model. It did not provide support for any of the "beyond the standard model" ideas that have been proposed over the last 40 years.

 

[stevendaryl]

The one experimental detail that seems like a tiny bit of departure from the standard model is the discovery of a small neutrino mass (I assume that the nonzero mass is pretty much accepted now?) But that's actually a trivial (I think?) modification of the standard model to accommodate nonzero neutrino mass.

 

[anorlunda]

I might agree that research on quantum interpretations or MWI is unlikely to produce anything. However, that research is certainly not a significant waste of research dollars. Theorizing at your desk is a LOT cheaper than building huge experiments. LHC, for instance, cost $13.25 billion to build, and then there's operating costs, computing costs to interpret the data, etc.

That's a very strange outlook on "significant waste." It is unlikely to produce anything but other stuff is more expensive. Where's Senator Fulbright when we need him?

If it was only a handful of MWI researchers, I wouldn't object, but there is no defined upper limit to the number of scientists worldwide who expect taxpayer financing for the same thing. How many QM interpretation researchers do we finance in the world today, 10³? 10⁴?

 

[stevendaryl]

That's a very strange outlook on "significant waste." It is unlikely to produce anything but other stuff is more expensive. Where's Senator Fulbright when we need him?

How else would you measure whether research is a waste of money? You compare how much money it costs to the likelihood of getting something valuable out of it. I think that Senator Fulbright was a little ridiculous in his criticism of research. He highlighted research that sounded silly, regardless of whether (A) it cost a lot of money, or (B) there was scientific reason to think that the research was worthwhile. I don't think he made any kind of careful cost/benefit study for research dollars.

If it was only a handful of MWI researchers, I wouldn't object

I think that it is only a handful of people who do MWI research.

 

[Dr. Courtney]

In my view, that much optimism is too much.

For example, I suspect that we will never be able to resolve which QM interpretation is correct, or what happened before the "origin" of the universe, Yet we have many scientists studying those things as a career. I just met a post doc at Dartmouth who is planning on spending the rest of his life on MWI. My reaction was, "What a waste of taxpayer money. He will likely never contribute anything to the state of the art in an entire lifetime."

I agree completely with your comments on MWI (and QM interpretations more generally) and questions of what happened before the origin of the universe. But I tend to be skeptical regarding whether these questions are even within the realm of science at all (the realm of science requiring testability). My comments about waiting long enough should be constrained to ideas where there is strong and clear testability to begin with. It was insightful of you to point out questions that I regard to be on the fringe of testability to begin with.

I recognize that you said, "If one waits long enough" and that is unbounded. In the future, we will have better methods and better tools and there is no defined upper limit to "better." But those might come from advancements in other areas like electronics, rather than from MWI scientists. Therefore the prudent policy would be to table some of those science investigations for several centuries until technology makes it possible to succeed.

For me, it depends on what you mean by "table." I agree that we should with hold public funding for ideas where the testability is decades or centuries in the future. However, I would strongly disagree with attempts to stifle thought and development of ideas where the proponents are able to find the funding independently of government. And I would also not prohibit "incidental" government funding like what a tenured professor does with his research time (unfunded other than salary) or publication costs like arXiv expenses and the like.

I might agree that research on quantum interpretations or MWI is unlikely to produce anything. However, that research is certainly not a significant waste of research dollars. Theorizing at your desk is a LOT cheaper than building huge experiments. LHC, for instance, cost $13.25 billion to build, and then there's operating costs, computing costs to interpret the data, etc.

I can appreciate that theorizing at one's desk is cheaper than huge experiments, but my value judgements would tend to reduce spending on theoretical ideas that I regard to be on the fringe of testability: string theory, MWI, pre-origin issues, etc. Theory grad students aren't much cheaper than experiment grad students, and computational needs of theory tend to be much more expensive than experiment (at least in atomic physics, blast physics, and ballistics where I have the most experience on both sides.) I'd relegate public funding on theories on the fringe of testability to faculty salaries, minimal publication expenses, and "borrowed" computing time on otherwise idle machines.

 

[PeterDonis]

The one experimental detail that seems like a tiny bit of departure from the standard model is the discovery of a small neutrino mass (I assume that the nonzero mass is pretty much accepted now?) But that's actually a trivial (I think?) modification of the standard model to accommodate nonzero neutrino mass.

As I understand it, yes, it is--basically you just add the right-handed neutrino singlet. AFAIK the only reason that wasn't included in the original Standard Model was that there was no experimental evidence for neutrino mass.

 

[stevendaryl]

I'm looking, and I can't find a pie chart breaking down the number of researchers in the various fields of physics, but I do know that nobody at my university worked on interpretations of quantum mechanics.

[edit] I should say, rather, that nobody was funded to work on interpretations of quantum mechanics. Some people (such as me, actually) worked on it in our spare time.

 

[fresh_42]

How else would you measure whether research is a waste of money?

I wouldn't measure it at all. To me this is a very, very American point of view, always having a return on invest in mind.

We value a thing called "freedom of research" here, which basically means, that we leave it to the researchers how they spend their time. Surely, things are different if you will occupy telescope time or accelerator time. But what happens on your desk is basically completely unregulated. Beside the research, university professors here have to teach for a certain weekly amount of time, and if they want to have a break from it, which is usually for half a year, sometimes a year if the attendance of a foreign university or the participation in some research groups are the reason, they will have to back up this request. However, the obstacles are negligible, a well written request usually will do.

 

[stevendaryl]

I wouldn't measure it at all. To me this is a very, very American point of view, always having a return of invest in mind.

Hmm. If you're going to spend money, surely you have to have some way of judging what's worth spending money on, right? You can't just leave a bowl with $10 million in it, and a sign saying: "If you need money to support your research, just take what you need."

 

[fresh_42]

Hmm. If you're going to spend money, surely you have to have some way of judging what's worth spending money on, right? You can't just leave a bowl with $10 million in it, and a sign saying: "If you need money to support your research, just take what you need."

Sure. But neither MWI nor QM interpretations need that bowl. They are both very theoretical, as math is, where my insights are basically from. What you need is a good library and maybe some money for new journals and research results. I explicitly excluded e.g. telescope time. But the "taxpayers'" money regarding MWI is simply financing the chair.

My point was the importance of "freedom of research" as we believe, that a close connection between research and funding will influence the results. Medical research is a good example for that. Therefore, we're no friends of such money related considerations.

 

[stevendaryl]

Sure. But neither MWI nor QM interpretations need that bowl. They are both very theoretical, as math is, where my insights are basically from. What you need is a good library and maybe some money for new journals and research result. I explicitly excluded e.g. telescope time. But the "taxpayers'" money regarding MWI is simply financing the chair.

Well, that's the point I was making to @anorlunda: the cost of MWI research is pretty negligible, compared to most other things.

 

[anorlunda]

I would strongly disagree with attempts to stifle thought and development of ideas where the proponents are able to find the funding independently of government...
I would strongly disagree with attempts to stifle thought and development of ideas where the proponents are able to find the funding independently of government. And I would also not prohibit "incidental" government funding like what a tenured professor does with his research time (unfunded other than salary) or publication costs like arXiv expenses and the like.

I agree with both of those statements. I wouldn't suppress speculative stuff, I would put a ceiling on the fraction of the science budget that goes toward speculative stuff. Figuratively speaking, 10² MWI researchers, but not 10⁴ (edit: add the words "supported by public money.")

We value a thing called "freedom of research" here, which basically means, that we leave it to the researchers how they spend their time.

What happens when the faculty wants to research flat Earth, cEold fusion, eugenics, bloodletting, or other topics that would harm the reputation of the institution? I wager that you would find a way to get rid of them despite "research freedom"

I agree that it is very American that we expect our taxes to be used for things we approve of, even in academia and science.

 

[fresh_42]

What happens when the faculty wants to research flat Earth, cEold fusion, eugenics, bloodletting, or other topics that would harm the reputation of the institution? I wager that you would find a way to get rid of them despite "research freedom"

This is an academic question. It won't happen. And of course the budget of such a person would be reduced to the minimum. Not sure how it is nowadays, professors used to have lifetime chairs. You don't need to quote absurdities. No publications, minimum teaching hours and alike are the real life equivalents, and yes, there are some of those from time to time, but it's not the standard, it's the exception. Btw, who paid the jet pack in the 60's? You see, it also happens in your system.

 

[Dr. Courtney]

I agree with both of those statements. I wouldn't suppress speculative stuff, I would put a ceiling on the fraction of the science budget that goes toward speculative stuff. Figuratively speaking, 10² MWI researchers, but not 10⁴ (edit: add the words "supported by public money.")

Well put.

What happens when the faculty wants to research flat Earth, cEold fusion, eugenics, bloodletting, or other topics that would harm the reputation of the institution? I wager that you would find a way to get rid of them despite "research freedom"

I agree that it is very American that we expect our taxes to be used for things we approve of, even in academia and science.

My view is that tenured faculty should be untouchable with respect to research interests. True and complete research freedom (bound only by applicable laws, not institutional sensitivities) pretty much is the motivation for tenure.

My view is also that government money needs to be controlled (at least in the US) through our established representative process. Sure, Congress does some stupid stuff, but I am loathe to create big scientific instutions with control over all the science spending without congressional oversight. When the scientific bureaucracies (NIH, NASA, NSF, DOE, DOD, etc.) get out of hand with how they are spending taxpayer money, Congress really does have the proper authority and power to reign them in, even if the process is imperfect.

 

[Dr. Courtney]

What happens when the faculty wants to research flat Earth, cEold fusion, eugenics, bloodletting, or other topics that would harm the reputation of the institution? I wager that you would find a way to get rid of them despite "research freedom"

This is an academic question. It won't happen. And of course the budget of such a person would be reduced to the minimum. Not sure how it is nowadays, professors used to have lifetime chairs. You don't need to quote absurdities. No publications, minimum teaching hours and alike are the real life equivalents, and yes, there are some of those from time to time, but it's not the standard, it's the exception. Btw, who paid the jet pack in the 60's? You see, it also happens in your system.

Emphasis added. I'm not sure it's a completely academic question. Creationist research pops up from time to time from secular institutions. There were a fair number of creationists in the science and math faculty at the Air Force Academy. Now, there's no way that this stuff would get Air Force or DoD funding other than the faculty member's salary. But faculty at USAFA had very broad leeway on what they published.

My wife and I published these two papers when she was on the West Point physics faculty. Not exactly creationism, per se, but my wife is an avowed six day creationist, and these two papers definitely are an attempt to pry open the epistemological door for belief in creation.

https://arxiv.org/ftp/arxiv/papers/0812/0812.4932.pdf

https://arxiv.org/ftp/arxiv/papers/0803/0803.4245.pdf

West Point expressed nothing negative regarding these two publications, and they were also listed on my CV when USAFA hired me a year later. I recall quoting the Bible in a couple of papers I published while at USAFA and the research office read them and approved them without the slightest blink. I won a teaching award and a research award and received two promotions in my four years at USAFA. They seem to get academic freedom. I didn't have a huge research budget at USAFA, but it was much larger than most science and math faculty get from the institution itself.

Edited to add:

Over dinner, my dear wife reminded me that when we were at MIT, the highly regarded Physics Professor David Pritchard (https://en.wikipedia.org/wiki/David_E._Pritchard ) engaged in research on alien abductions even hosting a conference at MIT on the subject. It didn't seem to hurt his funding or reputation.

See:
https://www.amazon.com/dp/0964491702/?tag=pfamazon01-20

 

[Lord Crc]

Counter-example: the Higgs mechanism.

Are you saying the Standard Model is more beautiful with the Higgs mechanism than without? I'm just a layman but my impression was that it was considered a necessary bolt-on at the time, rather than a beautiful extension.

Edit: That is, it may be the most beautiful way to extend the SM to give particles mass, but if that was not the driver would it have been accepted based on its beauty and with massive particles as a prediction?

 

[Dr. Courtney]

Research Freedom and Beauty

Shortly after Sep 11, 2001, my wife and I formed a small research business to answer some questions in ballistics related to quickly incapacitating terrorists. Throughout my career, my conception of beauty in physics always had a strong component of simplicity, but this is more in the sense of simple connections to experimental results rather than fundamental theoretical simplicity far removed from experiments. This aesthetic preference has served me well in atomic physics, ballistics, and blast physics. Since 2001, my idea of beauty in physics has also had a component of usefulness in counter terrorism. To provide myself with more time for research, I left my job at Cisco Systems and accepted a faculty position at a local college in Ohio, where the teaching load only required 25 hours per week, 32 weeks per year.

That job was much more about teaching than research, but there was a research section to complete on the annual reviews. Since our research would eventually lead to pubications and I had begun to use it to provide research opportunities to undergraduates at the college, I started mentioning it on my annual review paperwork in 2004 or so. In spite of the fact that the work was externally funded and conducted off campus, I began to get really negative feedback from the administration - comments basically saying, "No one here appreciates your work in ballistics, and it is not going to help your promotion or tenure process." I guess their ideas of beauty and academic freedom were a lot different from mine. By 2006, I had accepted a position at a different institution that was friendlier to reseach in support of counter terrorism and offered me $50,000 in research funds to accept the position.

 

[ZapperZ]

I'm surprised that no one has mentioned Ethan Siegel's take on this, and he did do quite a bit of an elaboration here.

https://www.forbes.com/sites/starts...r-best-living-minds-on-nonsense/#37078a27566e

Zz.

 

[stevendaryl]

I'm surprised that no one has mentioned Ethan Siegel's take on this, and he did do quite a bit of an elaboration here.

https://www.forbes.com/sites/starts...r-best-living-minds-on-nonsense/#37078a27566e

Zz.

The title doesn't quite mesh with the content of the review. Siegel isn't really saying that what the various unsuccessful programs--string theory, GUTs, supersymmetry, etc.---are nonsense. He's just saying (I think) that they haven't produced anything, and so maybe it's time to give up on them.

I wouldn't say that it's a matter of beauty considerations leading people astray, though. It seems more like that there are some mysteries about the universe that may never be solved, or may even not have a solution. You have a real-valued parameter in your model that could presumably be any real number, but it turns out that it is $10^{17}$. That's a mystery: why is it so big? But it might not have any answer at all, beyond: that's just what it is.

For some people, that's a bitter pill to swallow. But to me, the conclusion is just that some questions don't have solutions. It's not really a problem with a particular approach to looking for answers. To use the failure of these programs as an indictment of a particular approach to solving a problem, you would need to have evidence that another approach may have solved it. And so far, there isn't any evidence that there is any other approach that would have worked better.

So maybe the lesson is: Give up quicker? Or maybe it's: Pick mysteries to solve that are more likely to yield solutions in a reasonable time?

 

[fresh_42]

So maybe the lesson is: Give up quicker? Or maybe it's: Pick mysteries to solve that are more likely to yield solutions in a reasonable time?

This question is in the same category as whether people should stop taking part in the lottery.
The scientific answer was the one my mentor used to give: "Lottery is a special tax for idiots."
My friend had the economic reply: "The chances are low but so is the fee, so the small amount of costs justifies the risk."

Why is this the same? Because problems with expected solutions in a reasonable amount of time won't bring you the Nobel prize!

 

[Dr. Courtney]

This question is in the same category as whether people should stop taking part in the lottery.
The scientific answer was the one my mentor used to give: "Lottery is a special tax for idiots."
My friend had the economic reply: "The chances are low but so is the fee, so the small amount of costs justifies the risk."

Why is this the same? Because problems with expected solutions in a reasonable amount of time won't bring you the Nobel prize!

This is well put. I would add that all the physicists I know tend to have had some past successes with their aesthetic preferences on past problems, so we tend to have confidence that the same aesthetic preferences will work on future problems.

I also think I've learned to pick problems well suited to my aesthetic preferences, but this requires self-awareness both in what my preferences are and what kinds of problems they are well suited to. Hint: I don't pick problems where others with similar preferences and greater abilities have already been working hard and long and coming up empty. I pick problems where my preferences and approach are considerably different from what's been done and is not working well.

 

[Dr. Courtney]

The title doesn't quite mesh with the content of the review. Siegel isn't really saying that what the various unsuccessful programs--string theory, GUTs, supersymmetry, etc.---are nonsense. He's just saying (I think) that they haven't produced anything, and so maybe it's time to give up on them.

I wouldn't say that it's a matter of beauty considerations leading people astray, though. It seems more like that there are some mysteries about the universe that may never be solved, or may even not have a solution. You have a real-valued parameter in your model that could presumably be any real number, but it turns out that it is $10^{17}$. That's a mystery: why is it so big? But it might not have any answer at all, beyond: that's just what it is.

Given the 400+ year track record of mysteries having mathematical models, I think less than 50 years is a bit early to conclude that some mysteries relating to physical laws may never be solved. Perhaps more of a time to change tactics. We trained a generation of physicists with a narrow conception of beauty and naturalness that had worked pretty well for QED and the Standard Model. It may not be that beauty considerations are the problem. It may be that the same beauty considerations in which this generation of physicists were trained and guided is the problem.

 

[fresh_42]

Given the 400+ year track record of mysteries having mathematical models, I think less than 50 years is a bit early to conclude that some mysteries relating to physical laws may never be solved. Perhaps more of a time to change tactics. We trained a generation of physicists with a narrow conception of beauty and naturalness that had worked pretty well for QED and the Standard Model. It may not be that beauty considerations are the problem. It may be that the same beauty considerations in which this generation of physicists were trained and guided is the problem.

Sounds a bit like the patient who consulted a couple specialist and came back with as many diagnosis as there have been specialists - each one diagnosing along his lines of interest.

Unfortunately this concept of beauty is pretty simple and straight forward: Describe the system by differential equations and determine the symmetries aka invariants. That's it. In return this makes it difficult to get a foot into the door: there is simply not much place for what could be changed. I've recently read that there is a physicists who suggested to forget about Noether and symmetries. But how can you disregard such a fundamental concept? Not that he offered alternatives. (I made a thread about it then, but have forgotten what to search for now.)

SUSY is an (are) example(s) which always sounds to me as if it is basically the standard model plus some rather arbitrary generalizations: grade the algebra, increase dimensions, consider bigger groups, etc. I guess latest in $SL(1,000\,;\,\mathbb{C})$ you can find embedded whatever you want. To me as an absolute layman it always looks like shots in the dark hoping to hear something cry. Not very convincing.

 

[Vanadium 50]

Sorry for the slow response. Been out of the country and wanted to be complete.

For example, I suspect that we will never be able to resolve which QM interpretation is correct

We won't. The math is still the same in every interpretation, so there is no experiment that can - even in principle - tell us which interpretation is right. Indeed, "which interpretation is right" isn't a well-defined question. Interpretations are stories we tell ourselves as computational mnemonics, and we use them all the time in other subfields without thinking about them. ("Image charges", "heat flows", "virtual image", etc.)

Figuratively speaking, 10² MWI researchers, but not 10⁴ (edit: add the words "supported by public money.")

It's nowhere near this many. US-DOE supports maybe 200-300 theorists in total. The number supported to work primarily on quantum interpretations is, as far as I can tell, zero. If someone is funded to do some other thing and they write a paper on interpretations nobody is going to complain, but if that's all they are doing? No way.

Are you saying the Standard Model is more beautiful with the Higgs mechanism than without

I would say so. Spontaneous Symmetry Breaking is clever, and it happens in many different systems as well, e.g. ferromagnets.

That [the Higgs boson] was just a confirmation of the Standard Model. It did not provide support for any of the "beyond the standard model" ideas that have been proposed over the last 40 years.

I am old enough to remember when the Higgs boson was not part of the Standard Model. What is in the SM and is not in the SM has been retconned several times: I remember when massive neutrinos were in, but as soon as oscillations were discovered, out then went. Then oscillations become "the first sign of BSM physics". So that's not an argument I find convincing. Or even well defined.

But that wasn't quite the point I was making. One can't argue that billions spent to verify the Higgs mechanism is OK but billions spent to search for SUSY is not because it's the very same instrument so it's the very same billions. Similarly, if it's OK to have 50 years between proposal and discovery for the Higgs, shouldn't SUSY have until 2024? (I'm taking Wess and Zumino's paper as the starting point, although it's probably too early)

 

[PeterDonis]

What is in the SM and is not in the SM has been retconned several times

Yes, that's true; models develop over time so this is actually to be expected. My point was that when the Higgs was actually observed in the LHC, it had already been part of the SM for quite some time, so it wasn't "new evidence" that required changing any models, and it wasn't a sign of anything beyond the SM as the SM had been understood for quite some time. If the LHC had discovered the Higgs in, say, the 1970s, that would have been a different story.

I remember when massive neutrinos were in, but as soon as oscillations were discovered, out then went.

Do you mean "massless" neutrinos were in but then out? I thought the original SM had massless neutrinos, and the discovery of oscillations forced the change to massive ones.

One can't argue that billions spent to verify the Higgs mechanism is OK but billions spent to search for SUSY is not because it's the very same instrument so it's the very same billions.

I agree with this. I also don't think Hossenfelder was making the argument that it was OK to fund the LHC to find the Higgs but not OK for SUSY. I think she was just making the point that no predictions of SUSY have been confirmed thus far.

if it's OK to have 50 years between proposal and discovery for the Higgs, shouldn't SUSY have until 2024?

It's not a question of how much time passes, but whether experiments can probe the regime where the hypothesis being considered (such as SUSY) predicts that something new should be found. SUSY, or at least the versions of it that everyone seemed to be favoring, predicted that the LHC, operating at the energy regime it's currently in, should have found some supersymmetric particles. But it hasn't found any.