Friday, January 08, 2016

It's right when 150+ papers are quickly written on the diphoton bump

Adam Falkowski argued that 2016 will be the Do-or-die year, one that will decide about the character of the future of particle physics. The excitement is a sine-like periodic function of time and it is high now, much like it was high right before the LHC exploded in 2008 and when the LHC was discovering the Higgs boson in 2012.

(Yes, the peaks are multiples of four i.e. years linked to the leap years, Olympic games, and the U.S. presidential elections. Note that my words are probably more informative than his graph.)

Jester and several readers have also exchanged their opinions about the question:
Is it a sign of a pathology that three weeks after the inconclusive observations of the \(750\GeV\) bump by ATLAS and CMS, there are about 150 phenomenological papers explaining that? And is that an unhealthy manifestation of a hunt for citations?
I think it's totally fine if not cool if lots of models and arguments are invented by theorists that could account for the signal if the signal happens to be real. The papers show the state-of-the-art business of the phenomenologists, the kind of ideas that are still trusted or investigated, and they turn the people's brains on which is just great.

Yes, almost all or all the papers will turn out to be wrong. They're mostly mutually exclusive models. But that's how it works. When physicists are uncertain, they have to work on many possibilities and their number has to be high enough. One of the possibilities may turn out to be right. One doesn't need an insane amount of money or time to write a paper which is why it's not a problem when 149 papers that will be shown wrong are being written.

One should understand that the LHC has cost some $10 billion. If you assume that a physicist isn't doing anything else than writing papers on hep-ph, it costs about $10,000 to write one paper (a part of the salary, an order-of-magnitude estimate). So through the salaries spent on these papers on the diphoton bump, the taxpayers and institutions have spent something like $1 million so far. This is a negligible amount relatively to the cost of the LHC – not to mention larger expenses in the society – while the bump surely looks like a larger fraction of the "happiness produced by the LHC so far" than 0.01%.
Good ILC news: Japan has agreed to triple the workforce for the Japanese Linear Collider (J/ILC).
The papers are diverse in many respects. Some of them are kept close to the experiments and discuss signatures in somewhat model-independent ways; some of them are meant to be detailed string theory compactifications that should predict absolutely everything if they are true. And there are lots of degrees of grey in between.

The detailed models include non-resonant explanations for the bump, explanations with extra produced particles, explanations revolving around heavy axions, new pseudo-Nambu-Goldstone bosons, new symmetries, bound states in technicolor models, new Higgses in various extensions of a supersymmetric standard model, new fermions from grand unified theories running in loops, sbinos, sgoldstinos, radions and dilatons in theories with extra dimensions, many others, and combinations of some of these notions. String phenomenology has offered quiver models describing intersecting branes, some other braneworld models, models with old large dimensions, and both open strings or closed strings may matter.

One may worry that "almost each research direction" seems to have a way to "explain" the new signal so there are unavoidably lots of false positives. Indeed. But that's because the bump is rather generic. It hasn't told us much. There is a diphoton bump – the decay of a new ("totally neutral") particle etc. to two photons is something that many different models may get – and the invariant mass seems to be \(750\GeV\) – well, almost no models can unambiguously predict masses of new particles so to determine the qualitative features of models, the information about the mass conveys almost no lesson because the value is as good as other values (at least the nearby ones). All models that are remotely viable as explanations may adjust their parameters to agree with the observed value of the mass.

So it's fun to see what the people actually trust and what makes them excited. Some research directions in Beyond the Standard Model physics seem incapable to explain a signal of this sort. I actually think that their proponents should join the Diphotonfest as well and submit papers, perhaps papers arguing that their models predict that this resonance will probably go away. If such papers were published, we could have a much better idea about the thinking of all the people – a useful snapshot.

Is it strange that the papers came so quickly? Not really. The rumors have been out there for weeks before the CERN announcements. So some people have been working on papers for weeks. But right now, the time from the announcement is long enough so that the papers about the diphoton bump that are published these days could have very well been started after the announcement.

Are the authors hunting for citations?

Most of them probably are. They want to keep or get jobs and the job market is highly competitive. But is that wrong? I don't think so. It's normal. Many people – including those who say that they don't care about the money etc. – do care about the cash and this entity (and citations) motivate them to work hard enough. This is an effect that exists in almost all occupations. Bakers bake bread because they want the money they obtain when the sell the bread – even though there may exist bakers who do it because it's their religious mission. While we like to say that most/all physicists are idealists, and some of them surely are (do I have to tell you about a great example?), there are lots of people for whom it's a job, a way to make living, too.

Are the citation counts getting distorted?

Not much. Some bad papers may get a few citations just for "being a part of the avalanche" of the diphoton papers on phenomenology. But I don't think that people try to cite "all" other papers on the diphoton bump. At some moment, a selection unavoidably starts. The better papers do get a higher number of citations – at least, there will be a correlation making this proposition closer to "true" than to "false".

There is one point I want to make. The citation counts convey some information in high-energy theoretical physics. They're not perfect and no one believes they're perfect. But I think that all competent physicists agree that the citation counts are significantly positively correlated with papers' and people's contributions to the field. Those who deny any correlation like that or who think that the correlation is negative are just outright cranks. They have totally different opinions about everything simply because they don't understand physics at all.

Now, the correlation isn't perfect. And in some cases, most people could even agree about some mechanisms that distort the citation counts. But no one knows the "right" amount of credit that papers and people should be getting, anyway. If I – or someone else – have some opinion that the numbers should be much higher or much lower, it may very well be because I – or that someone else – misunderstand something; or have a distorted opinion about something. I think it's right for many physicists to be interested in "understudied" research directions – and to ask some bright folks and top big shots what is their opinion about the identity of these "cinderellas". But on the other hand, as long as the system basically keeps "at least mostly smart" people, it's just inappropriate for any individual to say that he or she has the "right opinions" about the value of all papers, unlike the rest of the community.

Researchers must be allowed to study things even if they disagree with each other. And indeed, if their disagreement becomes well-defined, they should publish papers about their alternative views, too. Such confrontations should proceed according to the standards of the expert community, not by some behind-the-scenes assassination attacks in the laymen's media etc. The experimental results and successes should still affect – and, assuming natural mechanisms, does affect – how much time, effort, and money is invested into the research of different ideas. But that doesn't mean that there should exist some "totalitarian" filter that allows specific people to completely suppress some kinds of research. Everyone should be modest enough to realize that when her opinions about the relative value of a research direction differ from the average "opinions of the community", it may be the community and not her who is closer to the fairest possible appraisal, after all.

(I used the word "her" in order to be politically correct.)

Fraction of hep-ph papers that are about the bump

On many days, the papers about the bump may represent 1/3 of the hep-ph papers. Is that too much? Too little? I don't know how to compute the absolute "right" percentage. But I think I know how to estimate the coefficient by which the activity focusing on some models should increase. If there is a viable signal of the global significance 2 sigma, i.e. 95%, it may be reasonable to say that the a posteriori probability of the models predicting such a thing increases by a factor of 20 relatively to the prior probability. For this reason, by Bayes' theorem, the number of papers about such models may increase by a factor of 20, too. As long as the probability is low enough, the number of papers dedicated to a certain possibility should be proportional to its probability (you get such rules from a cost-and-benefit analysis, I think).

If you assume that before the announcement, there could have been 1 paper about a model that would be making similar diphoton predictions below \(1\TeV\), it is justifiable to have 20 papers of this type a day after the announcement. I think that at this level, I agree with Jester's reader kal who also wrote:
I really don't understand the outrage sparked by the amount of theory papers on the di-photon resonance? What's the big deal? There is a speculative signal out there and people are working on it. If you ask me, this is much better than adding another prefix to MSSM or mentally masturbating about the holographic principle in 2+1 dimensions.
Kal also wrote another paragraph that I completely agree with: 50% of papers are good, 50% are not, and this seems to be the case even in the diphoton subset. And doing things that collect citations and jobs is legitimate.

Concerning the paragraph above: Well, adding a prefix to MSSM may be fun but it's safer to add the prefix just to SSM, like in E6SSM because the truly interesting, stringy, and capable of explaining the bump supersymmetric models are not really minimal and the focus on minimality is misplaced.

Also, I think it's more desirable to clarify the holographic principle as it affects the full-fledged, realistic spacetime we inhabit – the 10- or 11-dimensional one. So there's some reason why I would tend to agree with the specific criticism of the masturbations about 2+1 dimensions. Those 2+1D models are simply not quite realistic and they're toy models that belong to "mathematical physics" more than they belong to the standard particle physics.

But maybe kal would have included the 10- and 11-dimensional holography among the types of intellectual masturbation, too. Well, he or she would be completely wrong because these are some of the most important insights – and continuing research – in the physics of recent decades. However, this is the kind of the research that doesn't get directly amplified when a bump (or even a discovery) at the LHC is made.

Rastus Odinga Odinga wrote:
I agree that people writing papers about this is not a problem, though the speed with which the papers appeared was pretty laughable. What is really disturbing is that it is obviously so easy to come up with an explanation. As they say about religions, they can't all be right, but they can all be wrong.... the other disturbing thing is how boring all these papers are. Do we really want to have to start thinking about sgoldstinos? Is that a prospect that makes your pulse race? Do we really want something like technicolor to rise from the grave? YAWN!
I completely agree with an anonymous particle physicist's reply:
Holy cow, Rastus, if you're not excited by the possible discovery of the sgoldstino and what it implies you probably chose the wrong job.
Absolutely. The discovery of a sgoldstino would be absolutely stunning. Even the remote possibility makes my pulse race. Doesn't Rastus understand how completely amazing it would be? LIGO is probably going to announce the discovery of the gravitational waves – and people will agree that this is probably a clear Nobel-prize candidate. But it's still far from detecting individual gravitons. Sgoldstinos would be even more amazing, if they were discovered and shown to be almost certainly sgoldstinos, because they would be superpartners of superpartners of the gravitons.

It's greater than the discovery of gravitational waves by LIGO because one detects individual quanta; and one implicitly discovers supersymmetry, a totally new symmetry of Nature that would represent a comparable revolution in physics like Einstein's special and general relativity. And sgoldstinos would probably tell us something beyond the Yes/No answer about SUSY – something about the dynamics that breaks SUSY in Nature.

I am less excited about technicolor (because it's too similar a theory to those we know, like QCD) and I think it's less likely at this point (because the Higgs is light enough but not too light and because the substructure searches have shown no signals etc.). But if experimental evidence emerged that technicolor is relevant for particle physics, it would still be extremely important. What else Rastus is expecting or dreaming about if neither sgoldstinos nor technicolor have anything to do with the kind of insights that would make his pulse race? What makes his pulse race? And if nothing in particle physics does, why does he keep on appearing on particle physics websites?

Jester's discussion covers other topics, too. The \(2\TeV\) diboson signal isn't excluded yet but it doesn't seem "exciting" at this point. If we only had the aggreggate data with the year 2015 included, we wouldn't have gotten excited in the first place.

But back to the main topic.

I do think that the influence of the experimental hints on the phenomenologists' work is totally healthy – it's what one expects from a similarly large healthy subset of the scientific community. The bump has created an understandable excitement even now when it's inconclusive. And a significant fraction (a tenth or a quarter?) of the phenomenology community has already released a paper addressing the bump in one way or another. That's how things should be. Many physicists should actually have the expertise to react to actual questions that are suddenly posed to them (not questions they invented for themselves) such as "what is the most likely explanation of this bump if it is real?". And many of them do react.

Even if the bump will go away, this explosion of the activity will look like a healthy episode and fun. One may see how his colleague think about a rather well-defined problem. ATLAS and CMS have basically managed to persuade a big portion of the hep-ph community to solve the same homework exercise and it's good because people may immediately know how others think about exactly the same things.

Movements searching for non-existent diseases of science and the West

More generally, I think that too many people love to spread the "lousy mood" about ordinary things and business-as-usual in science and many other sectors of the human activity and it's just wrong. When it comes to high-energy physics, people should be excited instead of spreading their "lousy mood" and unjustified accusations about pathologies.

Let me mention one more recent example of the obsessive propagation of the "lousy mood". The notorious crackpot John End-of-Science Horgan wrote a tirade against Bayes' theorem. This is rather amazing because Bayes' theorem is nothing else than a quantitative explanation of the rational reasoning – especially about highly uncertain questions. Bayes' formula may be de facto rigorously proven. But Horgan doesn't like it because it "enables confirmation bias". What?

The whole theorem is about calculating the change of the probabilities that results from some new evidence or arguments. The theorem isn't just about the priors; it's about the ratio of posterior and prior probabilities. For example, above, I sketched a "Bayesian" estimate how much the number of papers about diphoton predictions should jump after the LHC diphoton announcements. This is a kind of an argument that wasn't common – it's about a vague, partly sociological issue.

But it's appropriate to use it if we want the most quantitative explanation why we're thinking in the ways we do. I mentioned that 20-fold increase only as a reaction to some claims that the avalanche of the diphoton papers was unjustified. I think it's justified and the Bayesian argument is an argument, something that my opponents don't seem to have at all. So I think that my arguments are in better shape.

Similarly, Joe Polchinski presents his Bayesian estimate that the probability that the multiverse is needed in physics is 94%. I wouldn't get the same figure. But I agree that the probability that some multiverse is needed cannot be correctly argued to be vastly smaller than 1%, for example. For him, it's greater than 50% which is surely a good reason for a fraction of the physics community to study this possibility. He only resorted to the Bayesian argument because it's a quantitative formulation of some arguments he is actually using or feeling – and because he wanted to show that his reasoning is more rational than the reasoning of the mindless anti-multiverse jihadists – and in this case, I surely agree with this "advantage Polchinski" even if my probability for the multiverse is below 50%. What he does may be described as reason – unlike what the critics do.

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