In this respect, nothing much has changed during the time when the blog was dormant, except that these sentiments are now firmly established. Crisis is no longer a whispered word, but it's openly discussed in corridors, on blogs, on arXiv, and in color magazines. The clear message from the LHC is that the dominant paradigms about the physics at the weak scale were completely misguided. The Standard Model seems to be a perfect effective theory at least up to a few TeV, and there is no indication at what energy scale new particles have to show up. While everyone goes through the five stages of grief at their own pace, my impression is that most are already well past the denial. The open question is what should be the next steps to make sure that exploration of fundamental interactions will not halt.

One possible reaction to a crisis is

*more of the same*. Historically, such an approach has often been efficient, for example it worked for a long time in the case of the Soviet economy. In our case one could easily go on with more models, more epicycles, more parameter space, more speculations. But the driving force for all these SusyWarpedCompositeStringBlackHairyHole enterprise has always been the (small but still) possibility of being vindicated by the LHC. Without serious prospects of experimental verification, model building is reduced to intellectual gymnastics that can hardly stir imagination. Thus the business-as-usual is not an option in the long run: it couldn't elicit any enthusiasm among the physicists or the public, it wouldn't attract new bright students, and thus it would be a straight path to irrelevance.

So, particle physics has to change. On the experimental side we will inevitably see, just for economical reasons, less focus on high-energy colliders and more on smaller experiments. Theoretical particle physics will also have to evolve to remain relevant. Certainly, the emphasis needs to be shifted away from empty speculations in favor of more solid research. I don't pretend to know all the answers or have a clear vision of the optimal strategy, but I see

*three*promising directions.

One is astrophysics where there are much better prospects of experimental progress. The cosmos is a natural collider that is constantly testing fundamental interactions independently of current fashions or funding agencies. This gives us an opportunity to learn more about dark matter and neutrinos, and also about various hypothetical particles like axions or milli-charged matter. The most recent story of the 21cm absorption signal shows that there are still treasure troves of data waiting for us out there. Moreover, new observational windows keep opening up, as recently illustrated by the nascent gravitational wave astronomy. This avenue is of course a non-brainer, already explored since a long time by particle theorists, but I expect it will further gain in importance in the coming years.

Another direction is precision physics. This, also, has been an integral part of particle physics research for quite some time, but it should grow in relevance. The point is that one can probe very heavy particles, often beyond the reach of present colliders, by precisely measuring low-energy observables. In the most spectacular example, studying proton decay may give insight into new particles with masses of order 10^16 GeV - unlikely to be ever attainable directly. There is a whole array of observables that can probe new physics well beyond the direct LHC reach: a myriad of rare flavor processes, electric dipole moments of the electron and neutron, atomic parity violation, neutrino scattering, and so on. This road may be long and tedious but it is bound to succeed: at some point some experiment somewhere must observe a phenomenon that does not fit into the Standard Model. If we're very lucky, it may be that the anomalies currently observed by the LHCb in certain rare B-meson decays are already the first harbingers of a breakdown of the Standard Model at higher energies.

Finally, I should mention formal theoretical developments. The naturalness problem of the cosmological constant and of the Higgs mass may suggest some fundamental misunderstanding of quantum field theory on our part. Perhaps this should not be too surprising. In many ways we have reached an amazing proficiency in QFT when applied to certain precision observables or even to LHC processes. Yet at the same time QFT is often used and taught in the same way as magic in Hogwarts: mechanically, blindly following prescriptions from old dusty books, without a deeper understanding of the sense and meaning. Recent years have seen a brisk development of alternative approaches: a revival of the old S-matrix techniques, new amplitude calculation methods based on recursion relations, but also complete reformulations of the QFT basics demoting the sacred cows like fields, Lagrangians, and gauge symmetry. Theory alone rarely leads to progress, but it may help to make more sense of the data we already have. Could better understanding or complete reformulating of QFT bring new answers to the old questions? I think that is not impossible.

All in all, there are good reasons to worry, but also tons of new data in store and lots of fascinating questions to answer. How will the B-meson anomalies pan out? What shall we do after we hit the neutrino floor? Will the 21cm observations allow us to understand what dark matter is? Will China build a 100 TeV collider? Or maybe a radio telescope on the Moon instead? Are experimentalists still needed now that we have machine learning? How will physics change with the centre of gravity moving to Asia? I will tell you my take on such and other questions and highlight old and new ideas that could help us understand the nature better. Let's see how far I'll get this time ;)

## 34 comments:

"SusyWarpedCompositeString..." theorists should think more about explaining the yukawas and coupling constants. If there's a desert, predicting the next decimal place in the SM parameters is one of the few places where novel predictions remain possible.

The center of gravity is Europe. China is growing, but its impact is comparable to a major European country.

Any links/examples in the new QFT formulations ? Thanks

Very well said and summarized the state of particle physics. What do you think of the status/future of HEP LATTICE?

There is also a discrepancy in the measurement of Hubble parameter in the small-scale observations and CMB (PLANCK) data, perhaps one should keep an eye on that as well!

Dear Anonymous,

Asia > China. Asia includes Japan, India, South Korea, Taiwan and many more.

Delighted to see you back. Why did you go away?

A nice essay, except that I was disappointed to see you plugging NAH's amplitudes. That's bullshit.

benji,

Basically spinor-helicity techniques, twistors, ampliuhedrons etc. This stuff dramatically simplifies the calculation of scattering amplitudes. Some suspect it could expose deeper subterranean connections in QFT.

Amanda,

NAH wasn’t the first to notice the power of twistors, etc. and he won’t be the last. Penrose, Hodges and a ton of others have been at this for a while now. Nothing about this is ‘bullshit’. It’s just a more sophisticated reformulation of what we already now. No extra assumptions aside form relativity and QM needed.

@Amanda:

To amplify the previous comment, there's loads going on in the amplitude field beyond amplituhedra (or spinor helicity for that matter). Some of this is already of direct relevance to higher order QFT computations in the standard model/QCD. Other stuff is more speculative and/or so highly dependent on susy that it will never connect to the real world. As a member of this particular cult, I do wish more people would work on developing and finding techniques that apply at least in principle to non-susy theories. As a mirror of what's happening in phenomenology I all too often see people keep beating a dead horse instead of trying to strike out in a new direction.

Doesn't non-0 neutrino mass give you a clue on what you may or may not expect at LHC?

If not, why was such a big deal made about non-0 neutrino masses and that its a first evidence of physics beyond standard model.

benji,

Indeed there is a lot to be understood, mostly in QCD and non-Abelian gauge theories where we are a lacking a proof of confinement, the spectrum of the theory and a proof of existence. This could have an impact in the way we look at a non-linear quantum field theory opening new insights into the Higgs sector that we know how to treat only perturbatively. E.g,, if you take a look at the Coleman-Weinberg mechanism you can realize that the idea could be good but the way you manage it through perturbation theory can lead you astray.

Benji: I recommend http://arxiv.org/abs/1708.03872

Aqeel: I don't have anything intelligent to say about lattice, but it's clearly an important ingredient of the precision program.

Shantanu: Neutrino masses is an evidence for new physics, which however could be as heavy as 10^16 GeV. A priori, no connection to the LHC.

so then why was non-0 neutrino mass results given nobel prize? Why did Pierre Ramond say that non-0 neutrino mass points to evidence for low energy supersymmetry?

See

https://physics.aps.org/focus/supplement/neutrinoquotes.html

Is the quote by P. Ramond not correct and we are as clueless about physics beyond standard model as we were before we knew about neutrino mass?

The first sentence is entirely correct. The second starts with some not-too-implausible wishful thinking, and ends with a huge leap of faith.

Jester, you say:

"...but also complete reformulations of the QFT basics demoting the sacred cows like fields, Lagrangians, and gauge symmetry."

Whatever the approach to a fundamental revision of QFT might be, it must fully recover the effective field theory in the infrared limit. As such, it cannot arbitrarily throw away fields, Lagrangians and gauge symmetries. Rather, it must successfully show that these concepts emerge from deeper principles (or a deeper framework of ideas) at the Standard Model scale.

"... at least to explain dark matter ..." I say that Milgrom is the Kepler of contemporary cosmology. I am not saying that Milgrom might be the Kepler of contemporary cosmology — I am saying that it's a fact based on overwhelming empirical evidence. Google "kroupa milgrom", "mcgaugh milgrom", "sanders milgrom", and "scarpa milgrom".

@Goldfain

basically, no. In every attempt at extensions along these lines people try to construct an engine that produces scattering amplitudes or correlation functions directly. Yes, you can *also* compute these with path integrals & Feyman graphs, etc, etc: this is considered one engine among many. Logically speaking, if tickling 10 unicorns in some way would yield LHC predictions which confirm those obtained with path integral technology, than the unicorn approach is physically equivalent. There is no physical need to directly derive path integrals from the unicorns, interesting an exercise this may be.

@ Rutger,

So, in your opinion, a fundamental reformulation of QFT should dispense of fields, Lagrangians and symmetries without recovering the SM physics in terms of these concepts?

@Goldfain

I think that a fundamental reformulation of QFT should dispense of fields, Lagrangians and symmetries *and* recover the SM physics

I think insisting that you want to reinterpret SM physics in terms of these concepts is not required.

@ Rutger,

Can you be more specific?

Please provide an example of a fundamental reformulation of QFT that meets two requirements:

1) discards fields, Lagrangians and symmetries from its conceptual structure,

2) successfully reproduces the full spectrum of SM predictions.

Hi, good to read this blog again.

To my own opinion, it looks like a coming stage of panic...

Btw, any news of the muon magnetic moment? I bet this one will be a success. I mean really new physics.

Best,

J.

Amplitudes aren't bullshit. But the amplituhedron surely is. SPACETIME IS DOOMED! DOOMED I TELL YOU! REPENT! REPENT!!

@Goldfain

Here’s a book by Elvang and Huang on this topic: https://arxiv.org/abs/1308.1697

As for your questions:

1. Start with unitarity and relativity

2. You get the irreducible representations

3. You get helictity spinors (for massless particles) and tensors (for massive particles).

4. Start constructing scattering amplitudes that transform correctly under the little groups and consistently factorize under unitarity,

5. With just these things, you can derive the existence of gravity, Yang-Mills etc.

6, Plug in the required couplings and viola, you can reproduce the entire standard model, at least at the perturbative level

7. The symmetries are embedded in the chosen couplings, this follows from step 5.

This paper nicely summarizes whole process: https://arxiv.org/abs/1709.04891

This is completely equivalent to the path integral approach, it’s just cleaner and simpler.

To be fair the analytic S-matrix type approach is to my mind currently missing a good understanding of renormalisation, and especially the renormalisation group equation and its cousins like Altarelli-Parisi. This is especially interesting given the topic of this post!

"Are experimentalists still needed now that we have machine learning?" What are you talking? It is much easier to replace theoretists than experimentalists. The job of a "theoretical high-energy physicist" is one of the first that will fall - because their naive human model-building can be done systematically and fast with machines.

Anonymous @ 6:11 and Rutger,

The formalism of scattering amplitudes in gauge theory and gravity is an exciting step towards replacing the traditional PI approach of perturbative QFT. However, it does not discard either quantum fields (spinor helicity implicitly assumes Dirac's theory) or symmetries (irreducible representations, the SU(2) little group implicitly assume group theory). From this standpoint, it cannot be considered a fundamental reformulation of QFT that throws away fields or symmetries from the outset. Besides, it remains to be seen if scattering amplitudes can successfully explain what SM leaves out (Dark Matter, Higgs naturalness, neutrino masses, baryogenesis, the replication problem, the origin of SM parameters and so on).

All this machinery of scattering amplitudes is always fundamentally based on perturbation theory, the only approach we know to treat QFTs. It is clear that the direction is not to improve the way we compute such terms but rather to find a different way to solve QFTs. Only this will help us to gain more insights.

One is astrophysics where there are much better prospects of experimental progress. The cosmos is a natural collider that is constantly testing fundamental interactions independently of current fashions or funding agencies. This gives us an opportunity to learn more about dark matter and neutrinos, and also about various hypothetical particles like axions or milli-charged matter. The most recent story of the 21cm absorption signal shows that there are still treasure troves of data waiting for us out there. Moreover, new observational windows keep opening up, as recently illustrated by the nascent gravitational wave astronomy. This avenue is of course a non-brainer, already explored since a long time by particle theorists, but I expect it will further gain in importance in the coming years.The importance of this can't be understated. The sheer volume of new data in astrophysics is stunningly large compared to HEP, there are many independent teams of investigators to limit group think, and the evidence being gathered is in the sweet spot where it is possible for theorists to make predictions than can't be tested when made but can be tested before the people making the predictions are dead. The wealth of data also purges theoretical dead ends that can't be disproven with existing data fairly quickly, preventing the field from reaching a tipping point where a majority of professionals in the field have an interest in experimental work not progressing so that their life work is not ruled out.

Another big factor for astrophysics is that we know for an absolute certainty due to dark matter and dark energy attributed phenomena that there is BSM physics to be discovered from this investment, while new HEP investment we can afford might or might not lead to new physics. And, while space based astrophysics observations aren't cheap, they are very cost competitive with a next generation collider big enough to potentially see something cool.

M-theory is the only theory thatseemsto have all the properties we would expect of a complete and consistent "history of everything," but that may just reflect our lack of imagination. If M-theory is correct, it predicts that every particle should have a super-partner. So far, we have not observed any super-partners, but the hope is that they will be found at the LHC. If they are discovered, it will be strong evidence for M-theory. On the other hand, it they are shown not to exist, that will be exciting, because we will learn something new.Quote from the Cambridge quantum Prometheus whose shadow has just faded on the classical spacetime scene but whose flame he stole for us from black holes is still enlightning the quantum theater. (bold emphasis is

his)In the mean time, a Princeton quantum Orpheus revives Von Neumann factors of type III from the underworld of algebraic and axiomatic quantum field theories... having no sufficient time unfortunately to explain for us in his crystal clear educational style, the marginal fact that Tomita-Takesaki theory is a keystone in the cathedral with two quanta of geometry patiently built and secretly offered to physicists by three musketeers: a retired from College de France mathematician, a son of Salam IHES theoretical physicist and one the most respected Russian cosmologist. With these two diamonds, found in the pocket of the Standard Model beggar, they can mimic dark matter and dark energy as a modification of the longitudinal mode in General Relativity and can also incorporate the idea of limiting curvature removing singularities... Maybe this new quantum of information will help high energy physicists to make the difficult task of conformal model building easier?

Remember dear physicist this almost forgotten knowledge from the past: Prometheus had a brother called Epimetheus!

I forgot to mention the "fourth musketeer" of this Solid Theoretical Research In Natural Geometric Structures adventure: Carlo Rovelli who is involved in another "marginal" fact also connected to the Tomita-Takesaki theory, this is the thermal time hypothesis proposed to explain the emergence of time in a hypothetical quantum gravity (QG) theory.

To quote Connes:

The [almost commutative] space-time which allows to recover the Sandard Model coupled to gravity is of type I, since it is the product of a manifold M by a finite space F i. e. a space whose algebra of coordinates is finite dimensional. It is not at this level that we expect to get "emergent time" but rather at the level of the algebra of observables in QG. The origin of this idea comes from Carlo Rovelli who --completely independently from the KMS story-- had found by reflecting about basic philosophical issues in QG that the "time we feel" (as opposed to a time coordinate in space-time) should be of thermodynamical nature and should be tied up to a thermal state: the heat bath of the relic photon radiation which breaks naturally Lorentz invariance. The real thing now is to put one's hands on a good model for an algebra of spectral observables in QG. Some ingredients towards this are explained at the end of our book with Matilde Marcolli [http://www.alainconnes.org/docs/bookwebfinal.pdf]).As far as the unfinished business of gauge fields unification is concerned it seems to me that some nonsupersymmetric Pati-Salam models can do the job as well as their SUSY counterparts up to the 10^16 GeV scale with three right-handed Majorana Neutrinos for successfull leptogenesis. Living with or without leptoquarks are alternatives that may depend on the Higgstory...

It happens by the way that thanks to the help of another 'fourth musketeer", Walter van Suijlekom, the noncommutative geometrisation of the Standard Model has delivered a minimal axiomatic framework, mathematically consistent (without conjecture), with powerful tools to

computethe full scalar and gauge fields from a spectral action principle provided the fermion content of the model is known.Last but not least it happens that, to quote Chamseddine:

by starting from a quantization condition on the volume of the noncommutative space, all fields and their interactions are predicted and given by a Pati-Salam model which has three.special cases one of which is the Standard Model with neutrino masses and a singlet field [the number of generations is put by hand]. The spectral Standard Model predicts unification of gauge couplings and the correct mass for the top quark and is consistent with a low Higgs mass of 125 Gev. The unification model is assumed to hold at the unification scale and when the gauge, Yukawa and Higgs couplings relations are taken as initial conditions on the renormalisation group equations one finds complete agreement with experiment, except for the meeting of the gauge couplings which are off by 4%. This suggests that a Pati-Salam model defines the physics beyond the Standard Model, and where we have shown [arxiv.org/abs/1507.08161] that it allows for unification of gauge couplings, consistent with experimental data

A final detail :

this discussion of spacetime geometry takes place in the Euclidean signature. Physics takes place in the Minkowski signature. The Wick rotation plays a key role in giving a mathematical meaning to the Feynman integral in QFT for flat space-time but becomes problematic for curved space-time. But following Hawking and Gibbons one can investigate the Euclidean Feynman integral over compact 4-manifolds implementing a cobordism between two fixed 3-geometries. Two interesting points occur if one uses the above spectral approach. First the new boundary terms, involving the extrinsic curvature of the boundary, which Hawking and Gibbons had to add to the Einstein action, pop up automatically from the spectral action as shown in [hep-th 0705.1786]. Second, in the functional integral, the kinetic term of the Weyl term (i.e. the “dilaton”) has the wrong sign. In [this] formalism the higher Heisenberg equation fixes the volume form and automatically freezes the dilaton... (arxiv.org/abs/1703.02470)From the theorist model-builder or the automaton-programmer, who could win the deep learning race off the Post-Naturalness

krisis(arxiv.org/abs/1710.07663)To last @Anonymus from the former Jester's post

"After the hangover"Useless > Useful ?

;-)

Missed you, Jester. Glad to see you back! Your blog is unique and thought-provoking.

Welcome back! we missed you Jester!

This morning, Shaposhnikov and Shkerin in https://arxiv.org/abs/1803.08907

" imagine that the Higgs mass arises purely due to some quantum gravity ffects. Having accepted the conformal invariance setting, this could only imply the existence of a non-perturbative mechanism driving the Higgs field vev towards its observed value, some 17 orders of magnitude below Planck mass."A Jacob's ladder from electroweak to a larger unification scale with some Higgs-Dilaton model?

Will they trigger a Springtime of Scalars ?

Sous les pavés, la plage (May 1968, Paris)

Sous les scalaires, l'unification (March 2018, Galois' birth village)

Proletarier aller Länder, vereinigt euch! (Februar 1848, Manifest der Kommunistischen Partei in London)

Scalars from all Scales, Unite! (March 2018, #ScalarsUp motto on Twitter)

Fluctuat nec mergitur (1358, Paris Motto)

Qu-operate and Fluctuate without Hindrance! (just before eternity, engraved at the Quantum Paradise Gateway)

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