Sabine Hossenfelder on the search for new particles

[strangerep]

If she was looking to improve the situation, she should have made more specific criteria for how she would rate "promising" vs. "unpromising" [...]

She has done this more than once in the past. In essence, she emphasizes the need to resolve inconsistencies between theory and experiment, or within theories that are already reasonably well supported by experiment. She has given several examples in earlier blog postings.

But most people never seem to remember that.

 

[PAllen]

I think she does in a way. Her argument echoes what Feynman noted decades ago: because of the success of the Standard Model, theory is driving experiment rather than the other way around. To her, all these hypothetical particles are largely a waste of time and money, theoretical particle physics is a dead field until a real new experimental result is discovered suggesting where and how to modify the Standard Model, and a dead field shouldn't be allocated so many resources. Woit noted in his blog post that the LHC ruled out "a lot of bad theory." Hossenfelder would argue those bad theories shouldn't have even been considered in the first place.

But where would this new result come from, if not from something like the LHC?

 

[PAllen]

She has done this more than once in the past. In essence, she emphasizes the need to resolve inconsistencies between theory and experiment, or within theories that are already reasonably well supported by experiment. She has given several examples in earlier blog postings.

But most people never seem to remember that.

One of the things she rejects as a good research area is the origin of matter/antimatter asymmetry. We should just chalk it up to initial conditions. This one I find quite absurd.

"Baryon Asymmetry and The Horizon Problem
These are both finetuning problems that rely on the choice of an initial condition, which is considered to be likely. However, there is no way to quantify how likely the initial condition is, so the problem is not well-defined."

from: "http://backreaction.blogspot.com/2019/01/good-problems-in-foundations-of-physics.html"

 

[malawi_glenn]

You missed at least one: https://arxiv.org/abs/2209.14882 (proposing a hypothetical new light Higgs boson in a new Higgs doublet to facilitate the possible existence of sub-GeV hypothetical DM particles in a thermal freeze out model of DM particle creation).

That is not a "2sigma-anomaly" paper in my book. It is a Dark Matter paper.

We is the collective community of physicists with power to govern how its institutions operate, i.e. the physics community.

When you write "we" you include yourself. And I do not think writing regularly on physicsforums counts...

The time spent writing the papers and the time by others reading the papers (who waits until publication to read papers anymore?), and not the make up of what gets actually published, is what causes the harm.

Is there really "harm" going on? As I wrote, I think this is overexaggerated. Sabine makes many claims with no backup like "talk to many particle physicsists in private..." and so on. There is no evidence, just anectotical observation on her behalf (and also on your).

ATLAS and CMS kick out a fair number of these "we looked for hypothetical particle X and there were no statistically significant deviations from the SM" papers every month.

That is true, but that is also powerful in a sense because the bounds can be made very strong for a vast majority of these goofy models in just a single measurement. This can in turn be the "cure" for these so called "anomaly" papers. These measurements are also quite model independent. How else are they going to find new particles or something deviating from the SM?
Let's go back to the LEP experiment. No new particle was found there, they basically did precision tests of the SM (like better W and Z mass etc). No Higgs. The urge of finding Higgs was very strong since there is a problem with having massive gauge bosons in a model. But where was Sabine back then? Why not just say that the entire framework of gauge symmetry in QFT is wrong in the first place and that particle physicsts need to spend their brain power elsewhere?

You think now since Higgs was discovered at LHC, they should just turn off the machine? Will that solve the problems in particle physics?

My personal view is that the most crucial research problem to solve in particle physics today is the origin of neutrino masses since it is not compatible with the SM. Neutrino masses are per definiton BSM physics.

 

[PAllen]

One of the things she rejects as a good research area is the origin of matter/antimatter asymmetry. We should just chalk it up to initial conditions. This one I find quite absurd.

"Baryon Asymmetry and The Horizon Problem
These are both finetuning problems that rely on the choice of an initial condition, which is considered to be likely. However, there is no way to quantify how likely the initial condition is, so the problem is not well-defined."

from: "http://backreaction.blogspot.com/2019/01/good-problems-in-foundations-of-physics.html"

And another, indicative of idiosyncratic interpretations of her own principles:

"
The Strong CP Problem
Is a naturalness problem, like the Hierarchy problem, and not a problem of inconsistency.
"
To me, flat out wrong. The existing best theory predicts x should occur. Experiment says it doesn't. This is an inconsistency between theory and experiment, the most important type of inconsistency to resolve.

 

[nuuskur]

I have mixed feelings.

Is she painting a(n inaccurate) caricature of particle physics and then proceeds to criticize its flaws? She said she used to be a particle physicist, but the way she expresses herself is like she was the end-all be-all scientist in that field and she would know Anything about it. I would not have expected such arrogance from a (former?) scientist.

 

[malawi_glenn]

I would not have expected such arrogance from a (former?) scientist.

https://www.fias.science/en/fellows/detail/hossenfelder-sabine/

 

[nuuskur]

I think it is incorrect to reason that: conjecturing particle X has been useless, because experiments have not yielded evidence for its existence.

I certainly don't believe that ALL particle physicists make up completely random conjectures (analogous to the twelve-legged spider) in order to write trivial nonsense papers about it. Mathematics, for instance, is cumulative and I'm sure (particle) physics has this property as well. Rarely does research start from a mostly clean slate.

 

[malawi_glenn]

I certainly don't believe that ALL particle physicists make up completely random conjectures (analogous to the twelve-legged spider) in order to write trivial nonsense papers about it.

Not even the majority, not even a large percentage either.

 

[pinball1970]

https://www.fias.science/en/fellows/detail/hossenfelder-sabine/

That was unexpected.

 

[artis]

I think these problems that Sabine talk about are fundamental to all complex fields. Look at any successful R&D lab or company, they will have x10 the amount of failed work as compared to the working ones.

Another example is patents, some 1% of all of them ever see daylight and ever get used.

That being said I think Sabine is at least part correct, because just like large companies and patents, it has became a game for them, they make thousands of patents each year where they know most of them are useless and will sit on a shelf, but they sort of put their foot in the door so that in case any other comes up with a similar but better idea in the future they can then claim in court that their intellectual property has been used and get some money.

In particle physics this would be analogous to what other users already commented that many physicists are pressed to earn credentials and money therefore they have to come up with something and can't just spend decades in silence trying to find that which in the end might not be there after all.But everything is easy from the start, recall the start of 20th century? All you had to do is make a vacuum and fire up an electron gun and produce some electrons , then hit an anode produce some photons and it was a "wow" moment, you could write articles about it, use it, patent it and the bonus is they were real particles that could be detected and put to use in industry etc, all were happy.
Nowadays any small incremental find is much harder and almost impossible to put to direct use.
Like we don't expect to use the higgs in industry or solve global warming with quark masses etc.
In theory in a free society you can't really command what others should spend their time researching, the only question then becomes if it's done with public funds, do we put some stronger checks in place to make sure the money is spent as best it can.
That being said on average I believe far more money is wasted on shady infrastructure and social program deals where the return on investment is just as bad as that in string theory.

 

[vanhees71]

She has done this more than once in the past. In essence, she emphasizes the need to resolve inconsistencies between theory and experiment, or within theories that are already reasonably well supported by experiment. She has given several examples in earlier blog postings.

But most people never seem to remember that.

The problem is that we don't have inconsistencies between theory and experiment concerning the Standard Model. The pattern usually is that there are some $4\sigma$ discrepancies with the standard model or some bump in some cross-section data, which after a while go away when the experimentalist got it to $>5 \sigma$. Another example is the muon $g-2$. There the before thought to be correct "theoretical prediction" (based on extrapolation of $e^+ e^- \rightarrow \text{hadrons}$ data to the corresponding hadronic off-shell contributions to $g_{\mu}$ via dispersive methods) has turned out to be most probably not accurate, which has been figured out by lattice-QCD calculations (the Budapest-Wuppertal group was first, but it's now consolidated by other independent lattice calculations). I'd say that's the usual way science works, and there's nothing to criticize about it. Also that there are many "theoretical speculations" like SUSY (only the minimal extension of the SM has been tested at the LHC and seems indeed not to be the answer for physics beyond the SM) or even string theory (without any relation to observables yet) is no argument against all this scientific activities since that's also how science works: You make a conjecture which can be tested by experiment, which then decides whether it's a valid conjecture or not. What I find a bit embarrasing, and here I agree with Hossenfelder, are the many completely weird speculations popping up like crazy on arXiv like the ones, e.g., after the apparent "faster-than-light neutrinos" of the OPERA collaboration. This went as far as claiming that the very basics of relativity were wrong, much like the usual crackpotery found by anti-Einstein afficionados sent to you via e-mail spam from time to time.

I also agree with Hossenfelder that it is very unlikely that a "grand new theory" or even a "theory for everything", solving the real physics problems (for me that's indeed basically only the quantum theory of gravitation), can be found by pure mathematical reasoning but that some new empirical input is really needed, i.e., some real discrepancy between the Standard Model and experiment, but as I mentioned above, there's no solid such observation yet. However, I don't see what else the HEP community should do than what she does, i.e., making ever better experiments as are done in the near future with the just upgraded LHC collider and the associated detectors. There are also no empirical hints at any quantum effects related to the gravitational interaction, which makes it the more difficult to find a right idea about this too. Here, I don't have the slightest idea, how this dilemma might be solved since also here GR seems to survive all tests under ever more extreme conditions, and all these tests naturally refer to macroscopic astronomical objects like neutron stars and black holes, where it is very unlikely to find hints at effects at the quantum level.

Where I completely disagree is that a solution should be to use even less solid philosophical quibbles about some pseudo-problems with the "foundations of Q(F)T". There are, of course, mathematical problems with Q(F)T, which are well worth to be investigated further, but to claim that there's a measurement problem or that one should derive Born's rule from something else, is completely misguided. I don't see any problems with these apparent "foundational problems". There's not the slightest hint that QT fails in describing any experiment today.

 

[malawi_glenn]

The problem is that we don't have inconsistencies between theory and experiment concerning the Standard Model

Neutrino masses says hello

 

[mfb]

Woit's page links to another page by Hossenfelder
http://backreaction.blogspot.com/2022/09/ive-said-it-all-before-but-here-we-go.html

That article is as absurd as the Guardian article. It even contradicts itself:

So my recommendation is that theory development should focus on resolving inconsistencies, and stop wasting time on pseudo-problems. Real problems are eg the lacking quantization of gravity, dark matter, the measurement problem in quantum mechanics, as well as several rather technical issues with quantum mechanics (see the above mentioned list).

Most of the models she criticizes are trying to do that. The others are trying to solve actual problems she dismissed as "pseudo-problems" for mysterious reasons.

More importantly, everyone can see that nothing useful is coming out of particle physics, it’s just a sink of money. Lots of money. And soon enough governments are going to realize that particle physics is a good place to save money that they need for more urgent things.

So everyone can see it, apart from everyone involved in it? Everyone can see it but we need Hossenfelder drawing attention to it?

If she writes these articles to help particle physicists, as she claims, why choose the Guardian? It's obviously not done to reach particle physicists. It's done to reach the largest audience she can get - people who cannot see through all the misrepresentations, half-truths, ambiguous statements and other problematic claims that make up the majority of the articles. The target audience for her books, which is conveniently mentioned at the end of the article.

I yet have to find a particle physicists who actually engaged with the argument I made.

That's an obvious lie, unless we let her dismiss any criticism as "that's not an argument", as she tries to do here:

The only “arguments” I hear from particle physicists are misunderstandings that I have cleared up thousands of times in the past.

So she actually admits herself that there is some discussion. But isn't it curious that she doesn't mention anyone who agrees with her? Or everyone only does so in secret? That's a pretty big conspiracy we must be in.

They almost all attack me rather than my argument.

Oh no, we call out people for writing obvious lies!

 

[nuuskur]

This pretense that she thoroughly understands particle physics and keeps putting words in others' mouths leaves a bad taste. It's more like a popularity contest. Inciting culty behaviour, I don't like it :(

..and I have this reaction when I barely know anything about her. It's not fair to prematurely judge, sure, but how seriously does she expect scientists and other relevant experts to take her when she weaves a narrative based on some cherry picked data? Worse, she is presenting to an audience of whom most are not equipped to critically assess her claims. Forming an echo chamber.

Being as uncharitable as I can for a moment - it's not important to her that she reach the experts at all. More followers, more potential people that buy her book(s). It definitely takes much less effort convincing people without some form of mathematical training.

 

[PAllen]

I'll add that years ago I used to have very good opinion of Hossenfelder, and still enjoy some of her papers. However, as she began seeking video stardom, she has more and more set a tone of poking at physicists who disagree with her not just critiquing theory or methods (while bemoaning ad hominem attacks on herself). The video that first turned me off was one where she said the LIGO team was doing crappy physics (her words exactly, in a public audience video) and that we should not believe what they say about their methodology in relation to the gamma ray burst coincidence event. (Also, strongly criticizing the Nobel award for any aspect of the LIGO work).

 

[vela]

So everyone can see it, apart from everyone involved in it? Everyone can see it but we need Hossenfelder drawing attention to it?

She's saying everyone, including the people involved in it, can see it, but particle physicists, both theoretical and experimental, have a vested interested in perpetuating the system as it keeps them employed.

If she writes these articles to help particle physicists, as she claims, why choose the Guardian?

I don't think she's trying to help particle physicists. If anything, she's arguing they need to go away and focus on what she considers real problems in physics. Her attitude and approach does come across as incredibly arrogant, and I can see why it rubs people the wrong way.

 

[PAllen]

I have mixed feelings.

e would know Anything about it. I would not have expected such arrogance from a (former?) scientist.

She is certainly a practicing productive physicist. She still averages 4 or so papers published in reputable peer reviewed journals (phys. rev, phys letters, and similar stature) per year.

 

[Vanadium 50]

Neutrino masses says hello

I think this is a bad example. The idea that "the SM predicts zero neutrino mass" came about only after they were known to be non-zero. I have another post here - somewhere - where I cite some before-and-after papers on this.

A better example of an unexplained phenomenpn is the neutrality of atoms. You can argue that the Higgs Yukawas, and CKM/PMNS matrix elements just "are what they are" with no better explanation than "well, they have to be something". But why are atoms neutral?

You can "explain" that by saying, it's because the electron has charge -1, the u-qaurk +2/3 and the d-quark -1/3, but again why? You can dig a little deeper, and conclude that the problem is not with weak isospin (because the generators are matrices) but with weak hypercharge (because a U(1) allows any real number as its charge): if quarks and leptons live in different representations of the SM, there should be no reason that their weak hypercharges be in small integer ratios with each other. (Ratio is 0:1:2:4:6)

Atoms are neutral to about 28 decimal places. You have two options - either this is just a 28 figure coincidence, or there is a reason for this. There is, as far as I know, exactly one idea for why this is: that the U(1) comes from breaking of a larger symmetry - for instance, SU)5) or SO(10). However, every group big enough to explain atomic neutrality also has additional particles. Should we:

1. Look for them?
2. Not look for them.

 

[mitchell porter]

if quarks and leptons live in different representations of the SM, there should be no reason that their weak hypercharges be in small integer ratios with each other. (Ratio is 0:1:2:4:6)

Anomaly cancellation?

 

[ohwilleke]

And another, indicative of idiosyncratic interpretations of her own principles:

"
The Strong CP Problem
Is a naturalness problem, like the Hierarchy problem, and not a problem of inconsistency.
"
To me, flat out wrong. The existing best theory predicts x should occur. Experiment says it doesn't. This is an inconsistency between theory and experiment, the most important type of inconsistency to resolve.

This is a misunderstanding of what the StrongCP problem is. The relevant equations of QCD would naturally have a place to put a parameter theta to describe CP violation, but the experimentally measured value of theta in a version of the equations to include this term at all, is zero (i.e. no CP violation).

The best existing theory does not predict that CP violation should occur. It merely observes that it could occur and does not. This is not a true problem.

The naturalness problem and the hierarchy problem are similar. These problems wonder why physical constants like the Higgs boson mass, have the values that they are physically measured to have, based upon the completely arbitrary assumption that certain kinds of physical constants ought to have a value on the order of one, rather than having very large or very small values.

But, these arguments are total bullshit. Nature faces no restriction on what value physical constants should take. The values that are measured do not contradict any laws of physics, they simply aren't what some misguided physics theorists think they should be in a theory that is obviously not right. Arguments that the laws of physics and their parameters SHOULD have values different than what they are are category errors, not parameters that misunderstand the nature of what science is.

 

[PAllen]

This is a misunderstanding of what the StrongCP problem is. The relevant equations of QCD would naturally have a place to put a parameter theta to describe CP violation, but the experimentally measured value of theta in a version of the equations to include this term at all, is zero (i.e. no CP violation).

The best existing theory does not predict that CP violation should occur. It merely observes that it could occur and does not. This is not a true problem.

The naturalness problem and the hierarchy problem are similar. These problems wonder why physical constants like the Higgs boson mass, have the values that they are physically measured to have, based upon the completely arbitrary assumption that certain kinds of physical constants ought to have a value on the order of one, rather than having very large or very small values.

But, these arguments are total bullshit. Nature faces no restriction on what value physical constants should take. The values that are measured do not contradict any laws of physics, they simply aren't what some misguided physics theorists think they should be in a theory that is obviously not right. Arguments that the laws of physics and their parameters SHOULD have values different than what they are are category errors, not parameters that misunderstand the nature of what science is.

I don’t look at it this way. Zero is not simply a parameter value, it is the absence of a phenomenon that could have any strength, for no known reason. Further, observed baryon asymmetry make one wonder why this is so. Thus, a credible theory that had strong force CP violations in an early era, with suppression later would solve two real problems at once. The whole notion of a self appointed arbiter of what problems are real is absurd.

 

[strangerep]

[Hossenfelder music video]... That was unexpected.

Yes -- she also composes music and has a separate youtube channel for that, iirc.

I like some of her music videos that I've chanced to watch (e.g., "The End of the World as We Know It" near the start of the panademic). But I don't bother visiting her music channel.

In any case, so what if she has other extracurricular non-physics interests? I've noticed plenty of people who seem unexpected peculiar if candidly observed in the wild.

 

[pinball1970]

In any case, so what if she has other extracurricular non-physics interests? I've noticed plenty of people who seem unexpected peculiar if candidly observed in the wild.

It was not a criticism it just took me by surprise.
Not at all what I expected when the video started.

 

[Vanadium 50]

Anomaly cancellation?

That's an effect, not a cause.

 

[Hornbein]

Note: Please read what she is talking about before commenting.

Have you no respect for Internet tradition?

 

[Hornbein]

Spoiler

Unkind people might say (theoretical) physics more like wanking...

Spoiler

... and now I wait to see if this will get past Berkeman...

Feynman said that about mathematics.

 

[malawi_glenn]

I think this is a bad example. The idea that "the SM predicts zero neutrino mass" came about only after they were known to be non-zero. I have another post here - somewhere - where I cite some before-and-after papers on this.

What is the lagrangian term for the neutrino masses in the SM then? Why do all the other fermions receive their mass by Yukawa coupling with the Higgs field and the neutrinos don't?

The values that are measured do not contradict any laws of physics, they simply aren't what some misguided physics theorists think they should be in a theory that is obviously not right. Arguments that the laws of physics and their parameters SHOULD have values different than what they are are category errors, not parameters that misunderstand the nature of what science is.

Zero is a particular value. Imagine you at the end of the every month had 0 USD on your account? Sure you got some salary, you paid rent, food, random purchases and so on, but you always ended up at 0 USD balance. Would you just accept it or would you try to look for an eventual cause of this phenomena?

Why is this parameter $\theta$ identical to zero in this term in the QCD lagrangian? $\theta F_{\mu \nu} \tilde F {}^{\mu \nu}$

Either it is identical to zero just by pure chance, or its very very very close to zero and we have not yet been able to experimentally to measure it (not enough statistics), or there is symmetry/mechanism for setting it to zero (axion models), or we do not understand how quantum Yang-Mills theories work. All of these options, except the first one, are open for scientific investigation.

Do we know of any other physical parameter that is exactly zero by chance?

Isn't physics also about finding new laws and patterns in nature? If it is just about conducting experiements and measure the values of things, it would be a pretty dull and weak field of science. For instance we would not have been searching for either the top-quark, or the Z/Higgs bosons.

In any case, so what if she has other extracurricular non-physics interests? I've noticed plenty of people who seem unexpected peculiar if candidly observed in the wild

I just thought that song was fitting to her article

 

[mitchell porter]

That's an effect, not a cause.

It's a constraint that the standard model has to satisfy, even without grand unification.

 

[malawi_glenn]

It's a constraint that the standard model has to satisfy, even without grand unification.

Question could then be why leptons and quarks have such hypercharges that SM is anomaly free in the fermion sector.
This was used as an argument to search for the top quark.

 

[vanhees71]

I think this is a bad example. The idea that "the SM predicts zero neutrino mass" came about only after they were known to be non-zero. I have another post here - somewhere - where I cite some before-and-after papers on this.

A better example of an unexplained phenomenpn is the neutrality of atoms. You can argue that the Higgs Yukawas, and CKM/PMNS matrix elements just "are what they are" with no better explanation than "well, they have to be something". But why are atoms neutral?

You can "explain" that by saying, it's because the electron has charge -1, the u-qaurk +2/3 and the d-quark -1/3, but again why? You can dig a little deeper, and conclude that the problem is not with weak isospin (because the generators are matrices) but with weak hypercharge (because a U(1) allows any real number as its charge): if quarks and leptons live in different representations of the SM, there should be no reason that their weak hypercharges be in small integer ratios with each other. (Ratio is 0:1:2:4:6)

Atoms are neutral to about 28 decimal places. You have two options - either this is just a 28 figure coincidence, or there is a reason for this. There is, as far as I know, exactly one idea for why this is: that the U(1) comes from breaking of a larger symmetry - for instance, SU)5) or SO(10). However, every group big enough to explain atomic neutrality also has additional particles. Should we:

1. Look for them?
2. Not look for them.

For non-Abelian gauge groups it's clear that the coupling constants within all particles must be the same, because already at the pure Yang-Mills Level the coupling constant is introduced, and then local gauge symmetry needs the same coupling constant to all other fields. For the Abelian U(1) (weak hypercharge/electric charge) there's no necessity on the classical level for the coupling constants to all fields to be equal.

However, when quantizing an Abelian gauge theory you must make sure that there's no anomalous breakign of the local gauge symmetry, and the chiral electroweak standard model is in danger from this side. The charge pattern of the quarks and leptons (together with the 3 colors of the quarks), however, makes the electroweak gauge symmetry indeed anomaly free. That's a somewhat weak argument though, because (if I remember right) there was a paper where someone ('t Hooft?) figured out different charge patterns, which also lead to freedom of anomalies.

Whether to look for particles of a hypothetical extension of the SM is not so easy to answer. I'm a bit skeptical, because if you have no good reason for any extension, because there's no discrepancy between the SM and data, it's pretty unlikely to really discover precisely the "new particles" predicted by any ad-hoc model you may have invented. On the other hand, I guess that such searches could help to discover at least something new, be it the "predicted" particles or something unexpected. For me somewhat an exception are axions, because they could explain the strong CP problem.

I think the current ideas about the future of experiments in HEP are well justified. One line is to exploit the newest upgrade and further future upgrades of the LHC to get higher-precision data about the known SM territory, particularly the Higgs with the hope that finally one really finds a robust signal hinting at physics "beyond the SM". Another line is to invest in more dedicated neutrino experiments, which is also well-justified simply because of all SM particles we know the least about the neutrinos (e.g., are they Majorana or Dirac fermions?).

 

[Astronuc]

That article is as absurd as the Guardian article.

I agree that it is poorly written, and largely defensive. Furthermore, it seems full of generalizations, e.g.,

There are several reasons why particle physicists can’t and don’t want to make this change.

That seems a broad brush reference to ALL particle physicists, rather than some.

Particle physicists, rather unsurprisingly, don’t like the idea that they have to change. Their responses are boringly predictable.

They almost all attack me rather than my argument. Typically they will make claims like I’m just “trying to sell books” or that I “want attention” or that I “like to be contrarian” or that, in one way or another, I don’t know what I am talking about. I yet have to find a particle physicists who actually engaged with the argument I made. Indeed most of them never bother finding out what I said in the first place.

That's an obvious lie, unless we let her dismiss any criticism as "that's not an argument", as she tries to do here:

I don't know that it is necessarily a lie, but perhaps she hasn't contact the entire field of particle physicists to get their take on her criticism(s). Perhaps she hasn't looked? Again, that seems an unfortunate generalization.

I have noticed how her books are promoted in her blog articles. I supposed a lot of 'celebrity' scientists, like many 'influencers', do the same. I also notice that she is a 'popular science' writer.
https://en.wikipedia.org/wiki/Sabine_Hossenfelder#Public_engagement_and_scientific_achievements

Nevertheless, is there any validity to any of Hossenfelder's statement(s)/criticisms(s)?
Ref: http://backreaction.blogspot.com/2019/01/good-problems-in-foundations-of-physics.html

By the way, I don't see her approach as being effective, but rather it seems counter-productive. I would think the first address her criticisms at a meeting of physicists in the field, or with some organization like AAAS or National Academy of Sciences.

It reminds me of the situation in nuclear engineering with the effort to develop sustainable, and more importantly, economically feasible controlled thermonuclear reactions (controlled fusion). Billions of euros/dollars spent, and it's still 10, 20, or more years away from 'reality', if ever. Popular science magazines tout it, researchers promote it, yet we aren't there yet. ITER is billions of euros/dollars over budget, and if it is successful, if it produces net (gain) in energy, i.e., energy output > energy input, it might be a modest gain. Officially, they are trying to "net energy", or Q > 1.

The world record for controlled fusion power is held by the European tokamak JET. In 1997, JET produced 16 MW of fusion power from 24 MW of heating power injected into the fusion plasma (Q=0.67). ITER is designed for much higher fusion power gain (https://www.physicsforums.com/javascript%3Avoid(0);), or Q ≥ 10. For 50 MW of injected heating power it will produce 500 MW of fusion power for long pulses of 400 to 600 seconds.

https://www.iter.org/sci/Goals

However, one must consider how efficient the conversion of the thermal energy will be converted to heating energy back into the reactor to sustain the fusion process.

In the area of fission, we have the Accident Tolerant (or now Advanced Technology) Fuel program and the Advanced Reactor Demonstration Program

https://nuclearfuel.inl.gov/atf/SitePages/Home.aspx
https://www.energy.gov/ne/advanced-reactor-demonstration-program
https://nric.inl.gov/

I expect many proposals to fail for technical and economic reasons.

 

[mitchell porter]

Maybe it's not widely known that charge quantization in the standard model follows, if you require cancellation of the mixed gauge-gravitational anomaly (e.g. see references 8-9 here). Maybe it's some kind of "swampland" principle (i.e. principle of quantum gravity), that U(1) charges are quantized, either by embedding in a GUT, or in "pre-broken" GUT multiplets?

 

[neilparker62]

https://www.fias.science/en/fellows/detail/hossenfelder-sabine/

Ah - all is revealed ! The problem with all these particles is that they're ... my brain .

I quite enjoyed following though:

 

[PAllen]

Nevertheless, is there any validity to any of Hossenfelder's statement(s)/criticisms(s)?
Ref: http://backreaction.blogspot.com/2019/01/good-problems-in-foundations-of-physics.html

I posted disagreement with two of these items in earlier posts. I also think the whole notion is dubious in that it a plus for the physics community that there is varied opinion on what are the promising lines of research. Thus, IMO, it would be a tragedy if funding bodies slavishly followed a prescription like that proposed in this link.