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Slow bottom-up HEP research is neither intellectually challenging, nor justified by the null LHC data

Ben Allanach has been a well-known supersymmetry researcher in Cambridge, England whose name has appeared a dozen of times on this blog and he wrote a guest blog on ambulance chasing.



Because of his seemingly bullish presonality, I was surprised by an essay he wrote for Aeon.Co a few days ago,

Going nowhere fast: has the quest for top-down unification of physics stalled?
The most nontrivial statement in the essay is
Now I’ve all but dropped it [SUSY at the LHC] as a research topic.
He wants to do things that are more bottom-up such as the bottom mesons (a different bottom, the Academia is full of bottoms). I find this description bizarre because SUSY at the LHC is a good example of bottom-up physics in my eyes – and the bottom mesons seem really, really boring.




Allanach wrote that other colleagues have left SUSY-like research before him, everyone has his own calibration when he should give up, and Allanach gave up now. One theoretical reason he quotes is that SUSY probably doesn't solve the naturalness problem – and aside from the absence of superpartners of the LHC, it also seems that SUSY is incapable of solving other hierarchy problems such as the cosmological constant problem. So if SUSY doesn't solve that one, why it should be explaining the lightness of the Higgs?




So he attributes all the null data – and the disappointment – to the top-down, "reductive" thinking, the thinking whose current flagship is string theory. He wants to pursue the bottom mesons and perhaps a few other "humble" topics like that. I think that I have compressed his essay by several orders of magnitude and nothing substantial is missing.

OK, his attribution is 100% irrational and the rest of his ideas are half-right, half-wrong. Where should I start?

In April 2007, I quantified dozens of (my subjective) probabilities of statements beyond the established level of particle physics. The probabilities go from 0.000001% to 99.9999% – and the items are more likely to be found near 0% or 100% because there are still many things I find "almost certain". But there's one item that was sitting exactly at 50%:
50% - Supersymmetry will be found at the LHC
Many bullish particle physicists were surely boasting a much higher degree of certainty. And I surely wanted the probability to be higher. But that would quantify my wishful thinking. The post above captured what I really believed about the discovery of SUSY at the LHC and that was associated with 50%, a maximum uncertainty.

By the way, with the knowledge of the absence of any SUSY at the LHC so far, and with some ideas about the future of the LHC, I would quantify the probability of a SUSY discovery at the LHC (High-Luminosity LHC is allowed for that discovery) to be 25% now.

String theory in no way implies that SUSY was obliged to be discovered at the LHC. Such a claim about a low-energy experiment doesn't follow from the equations of string theory, from anything that is "characteristically stringy" i.e. connected with conformal field theory of two-dimensional world sheets (more or less directly). Someone might envision a non-stringy argument – a slightly rational one or a mostly irrational one – and attribute it to string theory because it sounds better when your ideas are linked to string theory. But that's deceitful. Various ideas how naturalness should be applied to effective field theories have nothing to do with string theory per se – on the contrary, string theory is very likely to heavily revolutionize the rules how naturalness should be applied, and it's already doing so.

So Allanach's statement that the null LHC data mean something bad for string theory and similar top-down thinking etc. is just absolutely wrong.

A correct proposition is Allanach's thesis that for a person who believes in naturalness and is interested in supersymmetry because in combination with naturalness, it seems to predict accessible superpartners at the colliders, the absence of such superpartners reduces the probability that this package of ideas is correct – and people who have pursued this bunch of ideas are likely to gradually give up at some points.

It's correct but mostly irrelevant for me – the main reason why I am confident that supersymmetry is realized in Nature (at some scale, possibly one that is inaccessible in practice) is that it seems to be a part of the realistic string vacua. This is an actual example of the top-down thinking because I am actually starting near the Planck scale. Allanach has presented no top-down argumentation – all his argumentation is bottom-up. Any reasoning based on the naturalness of parameters in effective field theories is unavoidable bottom-up reasoning.

A mostly wrong is his statement that the null LHC data reduce the probability of supersymmetry. But this statement is justifiable to the extent to which the existence of supersymmetry is tied to the naturalness – the extent to which the superpartners are "required" to be light. If you connect SUSY with the ideas implying that the superpartners must be light, its probability goes down. But more general SUSY models either don't assume the lightness at all, or have various additional – never fully explored – tricks that allow the superpartners to be much heavier or less visible, while still addressing naturalness equally satisfactorily. So in this broader realm, the probability of SUSY hasn't dropped (at least not much) even if you incorporate the naturalness thinking.

You know, the SUSY GUT is still equally compatible with the experiments as the Standard Model up to the GUT scale. The null LHC data say that some parameters in SUSY GUT have to be fine-tuned more than previously thought – but the Standard Model still has to be fine-tuned even more than that. So as long as you choose any consistent rules for the evaluation of the theories, the ratio of probabilities of a "SUSY framework" over "non-SUSY framework" remained the same or slightly increased. The absence of evidence isn't the evidence of absence.

I think he's also presenting pure speculation as a fact when he says that SUSY has nothing to do with the right explanation of the smallness of the cosmological constant. I think it's still reasonably motivated to assume that some argument based on a SUSY starting point (including some SUSY non-renormalization theorems) and small corrections following from SUSY breaking is a promising sketch of an explanation why the cosmological constant is small. We don't know the right explanation with any certainty. So the answer to this question is "we don't know" rather than "SUSY can't do it".

But again, the most far-reaching incorrect idea of Allanach's is his idea that the "surprisingly null LHC data", relatively to an average researcher, should strengthen the bottom-up thinking relatively to the top-down thinking. His conclusion is completely upside down!

The very point of the bottom-up thinking was to expect new physics "really" around the corner – something that I have always criticized (partly because it is always partly driven by the desire to get prizes soon if one is lucky – and that's an ethically problematic driver in science, I think; the impartial passion for the truth should be the motivation). An assumption that was always made by all bottom-up phenomenologists in recent decades was that there can't be any big deserts – wide intervals on the energy log scale where nothing new happens. Well, the null LHC data surely do weaken these theses, don't they? Deserts are possible (yes, that's why I posted the particular image at the top of the blog post, along with a supersymmetric man or superman for short) which also invalidates the claim that by adding small energy gains, you're guaranteed to see new interesting things.

So I think it's obvious that the right way to adjust one's research focus in the light of the null LHC data is to make the research more theoretical, more top-down – and less bound to immediate wishful thinking about the experiment, to be less bottom-up in this sense! SUSY people posting to hep-ph may want to join the Nima Arkani-Hamed-style subfield of amplitudes and amplituhedrons (which still has SUSY almost everywhere because it seems very useful or unavoidable for technical reasons now, SUSY is easier than non-SUSY, for sure) or something else that is posted to hep-th or that is in between hep-ph and hep-th. Allanach's conclusion is precisely wrong.

You know, the bottom-up thinking expects something interesting (although, perhaps, a bit modest) around the corner. That is what I would also call incrementalism. But given this understanding of "incrementalism" (which is basically the same as "bottom-up", indeed), I am shocked by Allanach's statement
This doesn’t mean we need to give up on the unification paradigm. It just means that incrementalism is to be preferred to absolutism
Holy cow. It's exactly the other way around! It's incrementalism that has failed. The addition of new light particles to the Standard Model, to turn it to the MSSM or something else – so that the additions are being linked to the ongoing experiment – that's both incrementalism and it's what has failed in the recent decade because nothing beyond the Higgs was seen.

So a particle physics thinker simply has to look beyond incrementalism. She has to be interested in absolutism at least a little bit, if you wish. She must be ready for big deserts – a somewhat big desert was just seen. And she must "zoom out", if I borrow a verb from the Bitcoin hodling kids who want to train their eyes and other people's eyes to overlook the 70% drop of the Bitcoin price since December ;-). (For the hodlers, the word "she" would be even more comical than for particle physicists!)

But in particle physics, you really need to zoom out because the research of the small interval of energies around the LHC energy scale wasn't fruitful! Allanach also wrote:
But none of our top-down efforts seem to be yielding fruit.
This is complete nonsense – Allanach is writing this nonsense as a layman who has been away for decades or for his previous life so far. The top-down research in string theory has yielded amazing fruits. In recent 10 years as well as 20 years as well as 30 years, it has yielded many more fruits and much more valuable fruits than what the bottom-up research yielded. Allanach is probably completely unfamiliar with all of this – but this ignorance doesn't change anything about the fact that the quote above places him in the category of crackpots.

Ben, you should learn at least some basics about what has been learned from the top-down approach – about dualities, new transitions, new types of vacua, new realization of well-known low-energy physical concepts within a stringy realization, integrable structures in QFTs, new auxiliary spaces, solution to the information loss paradox, links between entanglement and wormholes, and many others. Unlike the papers presenting possible explanations for the \(750\GeV\) diphoton excess, those aren't going away!

There have been various positive and negative expectations about new physics at the LHC. Things would have been more fun if there had been new physics by now. People may feel vindicated or frustrated because their wishes came true or didn't come true. Their love towards the field or its subfields have changed and they may adjust their career plans and other things. But at the end, scientists should think rationally and produce justifiable statements about the natural world, including questions that aren't quite settled yet. I think that most of Allanach's thinking is just plain irrational and the conclusions are upside down. And he's still one of the reasonable people.

Also, Allanach seems to be willing to switch to things like "chasing hopes surrounding B-mesons, \(g-2\) anomalies, sterile neutrinos", and so on. Well, it seems rather likely to me that all these emerging anomalies result from errors in the experiments. But even if they're not errors in the experiment, I don't see much value in theorists' preemptive bottom-up thinking about these matters. If the experiments force us to add a new neutrino species, great. But immediately, it will be just a straightforward experimental fact. The theory explaining the data, if such an anomaly (or the other ones) is confirmed, will be a straightforward ugly expansion of the Standard Model that will be almost directly extracted from the reliable experiment.

My point is that the experimenters could almost do it themselves – they're the crucial players in this particular enterprise – and Allanach wants himself and lots of colleagues to be hired as theoretical assistants to these experimenters. But these experimenters simply don't need too many assistants, especially not very expensive ones.

Why should a theorist spend much time by doing these things in advance? What is the point of it? If such new and surprising anomalies are found by the experiments, the experimenters represent a big fraction of the big discovery. The only big role for a theorist is to actually find an explanation why this new addition to the Standard Model is sensible or could have been expected – if the theorist finds some top-down explanation! A theorist may find out that the existence of some new particle species follows from some principle that looks sensible or unifying at the GUT scale or a string scale; it's a top-down contribution. Without such a contribution, there's almost no useful role for a theorist here. A theorist may preemptively analyze the consequences of 10 possible outcomes of a B-meson experiment. But isn't it better to simply wait for the outcome and make a simple analysis of the actual one outcome afterwards? The bottom-up analyses of possible outcomes just aren't too interesting for anybody.

More generally, I would find some detailed research of B-mesons and the aforementioned anomalies to be utterly boring and insufficiently intellectually stimulating. I have always been bored by these papers – equivalent to some homework exercises in a QFT course – and it's close to the truth if I say that I have never read a "paper like that" in its entirety. I think that if most high-energy physicists abandon the big picture and the big ambitions, the field will rightfully cease to attract the mankind's best minds and it will be in the process of dying.

If most of the people in the field were looking at some dirty structure of B-mesons, the field would become comparable to climatology or another inferior scientific discipline which is messy, likely to remain imprecise for decades or forever, and connected with no really deep mathematics (because deep mathematics has little to say to messy, complex patterns with huge error margins). B-mesons are similar bound states as atoms or molecules – except that atoms and molecules have far more precisely measurable and predictable spectra. So if I had to do some of these things, I would choose atomic or molecular physics or quantum chemistry instead of the B-meson engineering! Like nuclear physics, subnuclear physics really isn't intellectual deeper than the atomic and molecular physics of the 1930s.

Fundamental physics is the emperor of sciences and the ambitious goals are a necessary condition underlying that fact. The experimental data should help the fundamental physicists to adjust their ideas what the ambitious goals should look like – but the experimental data should never be used as evidence against the ambitious goals in general! Experimental data really cannot ever justify the suppression of ambitions such as the search for a theory of everything. Everyone who claims that they can is being demagogic or irrational.

And that's the memo.

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