My Take On The Would-Be Particle At 38 MeV
By Tommaso Dorigo | August 22nd 2012 02:45 PM | 55 comments | Print | E-mail | Track Comments

I am an experimental particle physicist working with the CMS experiment at CERN. In my spare time I play chess, abuse the piano, and aim my dobson...

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Everybody seems to be talking about this new would-be particle, allegedly observed in diphoton decays in this paper by Kh. Abraamyan et al. at JINR, and consistent with an earlier claim of two physicists (van Beveren and Rupp) who had considered several distributions published by different collaborations. I will not discuss the story here since it has been done already in two posts here at Science 2.0, but rather provide guidance to those of you who trust my judgement.

And here it is: this is not a new particle. This is wishful thinking.

I first of all need to admit that I spent less than 15' on the original paper by van Beveren and Rupp to convince myself that this was not a result worth taking too seriously. I am sorry to be such a biased sceptic, but when it comes to bump hunting I have quite a bit of experience to sit on top of, and experience is something hard to hide in a closet and forget about.

Bump hunting requires rigorous checks of one's understanding of background distributions. This is a must, it cannot be done without. And it requires a-priori motivated selection cuts applied to the data: without this, researchers can tune the cuts and obtain bumps anywhere they like. And bump hunting requires one to demonstrate that one's detector has the required resolution, and show that the mass resolution is compatible with what is then observed. It requires a calibration of the mass measurement. It requires detailed Monte Carlo simulations - these could be waived forty years ago, not now. And it requires complex statistical analysis, which is not usually in the baggage of the average physicist. Well, none of the above is evident in the paper claiming the new boson. But let me first discuss the original van Beveren-Rupp article.

That whole van Beveren-Rupp paper is a list of blips and high-bins in complex invariant mass distributions, whose shape is absolutely not known nor justified by the authors. It seems like if you have a distribution such as the one on the right, which you have no idea what physics determines, you can instantly get enamoured with two high bins at 38 MeV or so, and that would constitute evidence for a new particle.

Or that, by subtracting off a Gaussian distribution (green histogram) from a mass distribution of dimuon plus dipion events reported by Babar (in black in Fig.2 in their paper, pasted below), one can make inferences about the residuals (in red in the lower inset). What on earth tells them the original distribution should be a Gaussian (it isn't, anyway; at lowest order it is a Lorenzian convoluted with a Gaussian, but higher-order radiative effects make it much more complicated, and systematical effects on the mass resolution make the Gaussian convolution non Gaussian anyway), the reader is left wondering. Not to mention that if one assumes that the energy scale is offset by 10 MeV the residuals completely change shape!

Okay, enough about the van Beveren-Rupp paper. Instead, the new claim is based on a real analysis (meaning that it is first-hand look at real data, and not a collage of second guesses on published results). What does the new paper (Kh. Abraamyan et al., "Observation of the E(38) Boson") show ? It is a study of diphoton events resulting from proton-target and deuteron-target interactions, collected by a spectrometer at JINR.

Deuterons in the beam have energies of 2 and 3 GeV, protons of 4.6 GeV. This low energy is of course quite adequate to study the low-mass spectrum of the produced photon pairs. I do not know in detail their detector (see a sketch on the right), so I have no means of speculating on the mass resolution they expect for photon pairs at small angle. From the sketch it seems that their cherenkov cells are situated at 355 cm from the proton target, but we do not know the dimension of the elements to make some inference on the angle resolution etc. Unfortunately, the paper does not spend many words on these crucial ingredients of any particle search.

They select photons in the same arm of their spectrometer, having energy above 50 MeV. Their sum is initially constrained to be in the 300-750 MeV range, and their angle satisfies cos θ < 0.997. The reason of these kinematical cuts is not explained to the reader, and I know that such cuts shape quite a bit the mass distribution of the two objects; the angle cut is probably meant to select photons in different detector elements, other cuts appear unmotivated.

One would expect that they control the expected shape of continuum background photons (arising from many processes, the most important being the decay of neutral pions and bremsstrahlung) with accurate methods, but alas, this does not appear to be the case. In the paper there is absolutely no discussion of how they determine the background. One is bound to blindly believe that it is perfect, unaffected by systematics, etcetera. Instead, authors proceed to fit the background-subtracted distributions they observe using a Gaussian shape. They do so for several sets of data coming from different reactions and different beam-target interactions. They change the energy and angle cuts of the photon pairs in each selection without explaining in any way the rationale of the choices.

At the end of the article they attempt, in truth, to put up some defence. They show a questionable reference signal of neutral pion decays to photon pairs, and produce a simulation which they compare to one of their background spectra. I would say this is far too little and too late to be taken seriously.

Finally, they produce fit results with a ridiculous number of decimal places. I am sorry to be blunt and a bit harsh, but this detail by itself shows they do not have a clue. If a student of mine comes in with a thesis containing a similar mistake, I am likely to kick him out of the door in no time ! A serious paper would never contain five decimal places in a fit mass error. Check it out on the left. (This is repeated several times in the paper).

In conclusion, I do not give much weight to this "find". And I am willing to bet $1000 that this claim will never be confirmed and accepted by the particle physics community. The discovery of elementary particles is a serious business, and the knowledge of mankind progresses with difficulty in the investigation of the subnuclear world. Care is required first of all in how the analyses are performed; but care is also required in explaining one's results and convincing the reader! Even if the boson at 38 MeV were true, authors of the new paper have failed spectacularly on the second, crucial task. Comments "The discovery of elementary particles is a serious business" It is stylish to drop the indefinite article in the above... "The discovery of elementary particles is serious business" "The discovery of elementary particles is a serious business" Deliberately omitting crucial information, viz. the huge signal in the COMPASS data, which was NOT explained by their Monte-Carlo simulation, is certainly NOT serious business. Dear George, as one of the authors cited in your Evidence paper, let me say this coram publico: we are sure that our MC simulation explains the signal. We also think that when preparing your Reply you didn't understand the MC we were showing in our Comment . The MC produces bumps in the same places as in RD without any tuning, and we can associate the individual thebumps with material in the spectrometer by simple geometry. There is, in our opinion, therefore no way that COMPASS data could support such a discovery. This is my opinion and all my colleagues I talked to on the subject agree with me, but I of course cannot speak on behalf of the collaboration (whose internal structure unfortunately prevented us from answering much faster to your claim of Evidence, not wanting to go through the process again we didn't prepare a reply^2). I agree with Tommaso in that yesterday's paper uses a background subtraction that looks like a typical case of wishful fitting. I'm also disappointed that they didn't cite my paper :-) Best regards, Tobias Schlüter Sorry, I wanted to put a link to our paper in there, but that didn't make is through, so here it is again arXiv:1204.2349. Dear Tobias, you're perfectly entitled to have your opinion, which I fully respect. But you cannot deny that your MC simulation has NOT shown quantitatively that the bump at 38 MeV in the COMPASS data is only an artifact. Regards, George P.S. I've given the relevant references in a comment below. Dear George, I think you agree that the MC produced a bump at 38 MeV, which we didn't put in. We also understand why there should be a bump. So if I understand the situation and your use of the word "quantitative" correctly, your complaint is that the height of the peak doesn't match the real data. This is something we didn't undertake: due to type of analysis the MC is used in, the MC is not tuned to reproduce the data 1:1, it is tuned to cover all of phase-space efficiently. We don't plan to do the quantitative work you seem to suggest, as we don't consider it fruitful. Best regards, - Tobi Thanks Yatima, this is a good suggestion! T. Thanks for your very interesting comments on the van Beveren - Rupp and Dubna papers. Do you think the COMPASS Collaboration at CERN will be able to check the Dubna measurements in the near future? I understand that COMPASS can use either a muon or a hadron beam, and they are using a hadron beam this year. Dear Chris, your question whether COMPASS "will be able to check the Dubna measurements" is a very "serious" one, in the language of Tommaso Dorigo, and most likely to any non-expert in this field, but probably not to Dorigo himself, who seems to be quite satisfied with COMPASS's decision not to further study the problem, since they don't consider it "fruitful" (Tobias Schlueter dixit), despite his admission that "Maybe there's a new particle." Indubitably, Tommaso Dorigo finds all this very "serious business". However, in my humble opinion it's just petty politics. Regards, George Dear George, it's not "fruitful", because if there's a new particle, COMPASS wouldn't be able to see it because of the relatively large backgrounds. For obvious reasons we simultaneously can't exclude that a new particle is there. There's no politics in this; maybe there is in your misrepresentations of what my colleagues and me are saying, but certainly not in our work. We understand that you looked at our plots when preparing for the Lisbon meeting in April, and we all know that you didn't bother checking with us before you posted your "Material Evidence" paper on the arXiv. That was a political decision on your part. I also assume that you consider a great political move your (or was it Eef's?) appearing on Portuguese prime-time news touting your discovery even though you were informed that we don't agree with your assessment. Do as you please, but don't make your problem our problem by misrepresenting our work. Best regards, - Tobi BTW for people who know Portuguese, here is the TV news appearance (9:50 AM, not prime-time) of one of the E38 discoverers: link to RTP archives. Dear Tobias, you simply postulate that "COMPASS wouldn't be able to see it because of the relatively large backgrounds", even if a dedicated search and analysis were carried out? Well, I still think that's a political decision, in the context of COMPASS management. Of course, it's perfectly legitimate, but I believe it's a big mistake, no matter if at the end of the day the E(38) turns out to exist or not. I'm not a religious person, so that I don't exclude any possibility beforehand. Regards, over and out. George Dear George, COMPASS simply isn't built for this type of discovery. We don't think that we can realistically obtain a clean spectrum in the gamma-gamma mass range below the pi0. This would certainly require removing virtually all material in the offending regions of the spectrometer. It would require changing noise-suppression cuts in our software. It would require extensive work modeling backgrounds in regions that we can suppress by simple cuts in our other analyses. At the same time we would want no decrease in tracking performance in order to suppress fake ECAL clusters and in order to obtain a well-defined reaction. The effect of all these modifications should be understood. OTOH an experiment of the type of the JINR experiment or CB-ELSA could answer these questions much easier. Therefore, there's very little incentive to do this work. Call that political if you will, I call it practical. Maybe there's a clear case why reactions such as pi-(190GeV)p -> E(38) pi- pi+ pi- p(slow) and p(190GeV)p -> E(38) p pi- pi+ p(slow) should be favored over anything JINR or CB-ELSA can do. I don't think you've made it. Regards, - Tobi The Russians have been finding bumps in their data since the bubble chamber era. They are (in)famous for it and nobody ever pays any attention to it. It looks like a new generation has gotten suckered into reading these papers. This opinion of Tommaso Dorigo certainly reflects the Standard opinion of experimentalists. It is based in a model-based knowledge of Nature, which has to be confirmed by experiment. Small effects are usually left out of consideration with the argument that it has too little statistics. Now, that latter issue is true for the present data, as we clearly state in our articles. But, since I do not have an accelerator in my office, I can only deal with already published data. Such data we have successfully analysed for meson spectroscopy in the past in many papers. However, in the papers where we talk about a possible boson at 38 MeV, we discuss a variety of too small signals, which all point in the same direction. So, one would expect a different reaction from experimentalist, namely furnish us with higher statistics data. So, that we can see whether the small signals hold, or disappear. The argument that we have too little statistics actually is that we do not dispose over better statistics data because we are not getting it from experiment. For example, figure 1 of Tommaso Dorigo. In the text of our article we say "Although with low statistics, one can observe a narrow peak in the CB-ELSA data centered at about 37 MeV. Clearly, the signal is too small to claim evidence of E(38), but it illustrates the possible decay mode E(38) through loops of virtual light quarks." Tommaso Dorigo is thus just repeating our conclusions. That is not helpful! Dear Eef, thank you for visiting, and sorry if I sound harsh. I have grown a reputation of speaking my mind here, so that is it... Your attempt to use published data to infer the presence of a new state is not bad per se, but it is too speculative for my taste, as I think I clearly expressed above. Indeed, I am part of the "mainstream", but I don't think my opinions can be labeled as groupthink. I think that showing a figure such as Fig.1 above in your paper is a big mistake. You do not make any attempt at explaining what is the expected shape of the background, so in that figure anybody with their own personal biases could read anything: a wide bump from 20 to 40 MeV, an interference effect at 50 MeV, or a large bump at 70 MeV, or two high bins around 35-40 MeV. Arguing that it is supporting evidence, if weak, of your claimed particle is, in my opinion, not science. I think you could have built your case more tidily if you had made a more careful effort to fit some of those distributions accounting for possible systematic effects. Why do you center a Gaussian in Fig.2 on the PDG mass rather than allowing it to move around ? If it moves even slightly, your difference plot will change swiftly. These kinds of checks are really what divides a wild speculation from a careful hypothesis testing. It is because of these technical aspects, and not because of my personal bias against non-SM light bosons (which, I admit, is still there) that I criticize your paper. Cheers, T. The large signal at 70 MeV is the onset of the neutral pion. Do I really heve to comment this to an experimentalist? Yes Eef, you need to explain that, and more than that. You seem to neglect to comment on the whole point I make in the post above, which is that a bump exists only with respect to a well-understood background prediction. Without a proof that one understands the background shape, any claim is worth zero. That is the sorry situation I summarized by putting those two figures in the article above. In summary, a paper claiming that there are hints of a new particle here and there is not worth the paper it is printed on, if it does not address the issue of background shape, normalization, uncertainty, and other systematics. That is just my humble opinion of course, but my advice is to not neglect it - it is shared by many colleagues. Cheers, T. Angry again? Good morning. Here some more detail of the CB-ELSA data. As you can see for yourself the neutral pion signal sets out at about 60 MeV. But, you could of course also have a look at Eur.Phys.J.A33, 133. Cheers, Eef Since the img thing did not work, here is the link: http://cft.fis.uc.pt/eef/CBELSAfig6b.jpg In the first place, I really appreciate your feedback! But, now let us go to real business. Experimentalists seem not to have observed (except for a remark in a BaBar paper http://arxiv.org/abs/0809.4120 , page 6, 2nd column, 2nd paragraph), threshold enhancements. In the analysis one uses very old expressions which work well for the light flavors, but certainly NOT for the more massive quarks. Consequently, several "bumps" are baptised "new particles". We have "discovered" this effect in http://arxiv.org/abs/arXiv:0706.4119 (reasonably well summarised in the Appendix at page 12). A more compact notation of the formalism can be found in http://arxiv.org/abs/arXiv:0710.5823 . Although I do not claim to have solved the issue, we have given it a try in http://arxiv.org/abs/arXiv:0908.0242 in which article we show that bumps like the X( 4660) and the Υ(10580) are non-resonant threshold enhancements. The real resonances can also be found. The ψ(5S,4D) are pinpointed in http://arxiv.org/abs/arXiv:0908.0242 , but the response of Belle is that WE (meaning, of course, instead, Belle) have not enough statistics. Nothing is done to clarify that! The Υ(4S) we find at 10.735 GeV in http://arxiv.org/abs/arXiv:0910.0967 (see also http://arxiv.org/abs/arXiv:1010.1401 ). No further attempt of experimentalists to clarify that situation. It is clear to everybody, of course, that the vector mesons are central in the search for the structure of the meson spectrum, because they can cleanly be produced in electron-positron, contrary to mesons with all other quantum numbers. So, a good knowledge of the vector meson spectrum is vital to hadronic physics. However, not all channels are suitable. Also that we have tried to explain to our colleagues experimentalists in http://arxiv.org/abs/arXiv:1005.1010 , or in http://cft.fis.uc.pt/eef/Frascati2010talk/depletion/octopsi.htm . But, no further follow ups! We have quite some list in the mean time of non-resonances, stated to be "particles" in the Review of Particle Physics. Below, a list of vector resonances which urgently need much more statistics: are the ψ(3D) to ψ(8S) resonances: http://arxiv.org/abs/arXiv:1005.3490 5S and 4D http://arxiv.org/abs/arXiv:1005.1010 3D http://arxiv.org/abs/arXiv:1004.4368 3D 5S 4D 6S 5D 7S 6D and 8S http://arxiv.org/abs/arXiv:0904.4351 3D 5S 4D 6S and 5D http://arxiv.org/abs/arXiv:0809.1151 5S 4D 6S and 5D We, furthermore pinpointed clearly two more Υ vector resonances, namely the Υ(2 3D1) http://arxiv.org/abs/arXiv:1009.4097 (with enough statistics to be considered for the Review of Particle Physics) and the Υ(4S) http://arxiv.org/abs/arXiv:0910.0967 . In my talk http://cft.fis.uc.pt/eef/Frascati2010start.htm I have paid a lot of attention to those issues (in the 20 available minutes and for a large audience of experimentalists). Not giving priority to those subjects means that one can ad infinitum continue with all kind of non-sense models, some of them referred to as mainstream. Dear Eef, to make things worse, when statistics seems abundantly present, like in the COMPASS paper http://arxiv.org/abs/1108.6191 (Fig. 1, left; also see our eprint http://arxiv.org/abs/1202.1739 , Fig. 8), COMPASS tries to argue away ( http://arxiv.org/abs/1204.2349 ) 46,000 events, with a Monte-Carlo simulation that does not even remotely resemble their own measured data ( http://arxiv.org/abs/1204.3287 ). But of course, it's much easier and safer to ridicule the Monte Carlo of a small bunch of guys at Dubna than doing the same concerning hundreds of neighbours at SPS. Well, if that's seriousness, I'd rather be unserious. Groetjes, George The point of showing that MC study in our preprint on behalf of COMPASS was not to reproduce the data, it was to show that our standard MC produces bumps right where you claim a new particle. We also understand the origin of the bumps, independent of MC. Maybe there's a new particle, but the visible bump is definitely due to detector material. Best regards, - Tobias Schlüter (on his own behalf) Hi Tobias, nice to hear from you. Same with us. I am convinced that there is something at 38 MeV. You don't think so! But you are on the safe side. Nevertheless your artefact only explains about 10 percent of the measured signal. Consequently, 90 percent still needs an explanation! Greetings, Eef Dear Eef, I don't recall the details, but I remember that you added to our MC plot a pi0 peak, even though there already was one, with a shape that you assumed. Therefore I don't think that your 10%/90% are quantitative results. Regards, - Tobi But I recall! There was no neutral pion in your MC. That was even agreed with Jan Friedrich at our meeting in Lisboa! So, sorry, my "estimate" is quite accurate. Jan leaves for vacation today, so he's probably not going to answer, but I know very well that there's a pi0 in the MC. That said, I looked at the plot in your Reply again. You overlaid the experimental plot for pi- p -> pi-pi+pi-gamma gamma p with the MC for p p -> p omega (-> pi- pi+ gamma gamma) p. There's no way you could make a quantitative statement based on that, as you're comparing apples to oranges. Given the nature of our MC (which is phase-space distributed due to the analysis technique), even in the same channel it would be a comparison of boskop to granny smith. Cheers, - Tobi Yes, you are almost right! However, in the last figure of our Reply We compare apples with apples! Regarding the neutral pion: Just look at your pictures and then tell me where the neutral pion appears. Moreover, the signal at about 10 MeV has nothing to do with your MC. It seems that you are comparing apples with pears. It's near the right edge, we cut the spectrum where it sets on so that the vertical scale remains reasonable. Resolution is slightly better in MC than in RD, which is why you see the onset of the peak in RD but only barely in MC. We take this into account in the analysis. This of course distorts your vertical scale, and thus the relative height of the structures on the left. Ah, sorry, yeah, I stopped when I saw the figure where you compared dislike things and didn't scroll further down. I now remember this a little more clearly. Instead of going through all the details of our simulation, I think we can agree on the following: 1) it is clear that the evidence in the COMPASS data is much less clear than you made out in your preprint titled "Material Evidence of a 38 MeV Boson", because 2) there is a bump near 40 MeV that is due to detector material in the COMPASS spectrometer 3) there are other, larger effects that are not accounted for in the COMPASS simulation such as the left edge of the spectrum 4) a simulation including backgrounds will certainly increase the left edge of the spectrum The neutral pion from your MC is not visible! Now you say that your MC is incomplete. I don't think that Jan Friedrich will be happy with all this. He was even worried that we would publish our reply! The neutral pi0 is there. See the rightmost figure in our Fig. 3, where it's clearest, and your reply to Tommaso above. Since we only wanted to show that material leads to bump in the low-mass range, we didn't bother tuning the MC data to match the data one-to-one. This tuning is also not needed (nor correct) for the type of analysis undertaken. I just got hold of the person who did the MC. She tells me the following: """ The pi0 is not absent at all, the reason why it is not seen is because the MC is for 2009 with a much better resolution and then you have to extend the figure much more to the right to see it. 2009 MC and RD give pi0 widths which agree well in both calorimeters but these figures were not released. """ The RD in the picture is from 2008 (for which a separate MC was undertaken, as she explains further down in her mail). So that explains why the pi0 peak is slimmer in MC than in RD, sorry that I was confused before. The change in resolution is due to different reconstruction codes, material distributions are virtually the same between 2008 and 2009. This opinion of Tommaso Dorigo certainly reflects the Standard opinion of experimentalists. It is based in a model-based knowledge of Nature, which has to be confirmed by experiment. Small effects are usually left out of consideration with the argument that it has too little statistics. Now, that latter issue is true for the present data, as we clearly state in our articles. But, since I do not have an accelerator in my office, I can only deal with already published data. Such data we have successfully analysed for meson spectroscopy in the past in many papers. However, in the papers where we talk about a possible boson at 38 MeV, we discuss a variety of too small signals, which all point in the same direction. So, one would expect a different reaction from experimentalist, namely furnish us with higher statistics data. So, that we can see whether the small signals hold, or disappear. The argument that we have too little statistics actually is that we do not dispose over better statistics data because we are not getting it from experiment. For example, figure 1 of Tommaso Dorigo. In the text of our article we say "Although with low statistics, one can observe a narrow peak in the CB-ELSA data centered at about 37 MeV. Clearly, the signal is too small to claim evidence of E(38), but it illustrates the possible decay mode E(38) through loops of virtual light quarks." Tommaso Dorigo is thus just repeating our conclusions. That is not helpful! The 38-MeV Schlüteron must be the original axion (as opposed to the lighter axion hoped for these days). No doubts! Hurrah! I like that name. Reminiscent of the controversy surrounding an e+e- bump "seen" in low energy heavy ion collisions many years ago. See below for last reference known to me. Tommaso has not noted (relevant?) that the targets are C and Cu. Paper: nucl-th/9703006 Title: APEX: Positive evidence for sharp 800 keV pairs from heavy ion collisions near the Coulomb barrier Authors: James J. Griffin (Physics, U. of Maryland, College Park, MD.) \\ The best fit to the published APEX U+Th data describes a sharp line of 123 pairs of width 23 keV at 793$\pm\$7 keV; also, the data impose a positive
99.0%CL lower bound of 23 sharp pairs. It is therefore untenable to argue
from the APEX data against the existence of sharp pairs. Data-only ratios
APEX/EPOS pair counts show empirically that the two experiments' pair data
are mutually consistent and of comparable statistical potency: conflicts, if
any, can be resolved only by other independent evidence. A perspective is
offered on the current status of the Sharp Lepton Problem, and alternative
non-heavy-ion experimental approaches to it are recommended.

Funny, I remembered a remark from a recent lecture of Robert Shrock: "With fπ ∼ 93 MeV, this yields mW ≃ 30 MeV, mZ ≃ 33 MeV". But of course, it is usual lore. See Phys. Rev. D79, 096002 (2009)

Tommaso, do you think that any of the LHC experiments could say anything about this "particle"? Perhaps ALICE, using the HI runs?

Hard to resolve a 38 MeV "structure". Not a problem of what beams we use. Rather, the signature of two close by photons. The problem, as I see it, is that it is not a high-priority task to exclude it.

Cheers,
T.
As far as I am informed by ATLAS people, there are just too many low-energy photons which makes it hardly possible to single a two-photon spectrum out of it.

Come on, I do not believe this for a minute. Both ATLAS and CMS have produced pizero peaks with a millionth of the data available now, after the first days of low-luminosity running. Anything that is produced strongly as the particle you claim, at a mass of 38 MeV, would have such a high cross section that finding a peak would not be hard.

Please note that if one fears that photons have too much noise background, one can revert to conversions (e+e- pairs), which are cleaner at low energy

Cheers,
T.
A. Reis (Feb 2012): The two-photon channel for us is ruled out: way too many low energy photons.

Here, is an example of LHCb http://i.stack.imgur.com/qgLWD.gif
Now, one would need 0.5 to 1 MeV bins and a lot more statistics.
But, indeed, it could be done!

I have estimated that one would need about 50.000 times more two-photon events than in the LHCb pi-zero spectrum, in order to reach COMPASS-level accuracy. Is that feasible?

Dear Eef,

as I said it is not a problem of statistics. The plot you link was probably done with a ridiculously low integrated luminosity. The problem if you want is to find a good sample of low-pileup data. One can take minimum bias triggers, for example, from the end of runs. I will fetch a pizero plot from CMS if I find it.

Cheers,
T.
Here is e.g. a pizero mass plot from the first few weeks of 7 TeV running.

As you see there are almost two million reconstructed pizero->photon pairs, in a very small part of the total data available. If one wanted to do it seriously, in the full 2011+2012 dataset I believe one could reconstruct of the order of several hundred millions of them. Also note that the spectrum does not die out at low mass: a 38 MeV bump would certainly have not escaped us.

Cheers,
T.

I am going to post a paper on the arXiv where I demonstrate that, if one subtracts the MC prediction from the data in our pi0 plot above, one gets a clear sinusoidal waveform which I can fit with a truly marvelous theory of mine, which this margin is too narrow to contain.

By the way, in Kh. Abraamyan et al., not only the number of decimal places is ridiculously large, but it is even inconsistent: 38.4935+-1.02639 has 4 digits in the central value, and 5 in the uncertainty.
It really looks like a mindless dump of whatever came from "cout", with no attempt at formatting.
Probably not ignorance, but sloppiness.

Thanks, that looks very promising indeed!

To Andrea Giammanco: Looking forward to your paper. Please keep me informed. In the mean time, you could have a look at http://arxiv.org/abs/arXiv:1009.5191 .
As far as the Dubna result is concerned. They have promised to come up with a description of their experiment and methods of analysis very soon. We just have to wait a bit more.

Dear Tommaso,
After studying the CMS result better, I have one comment.
The pi-zero resolution is not very good, comparable to the resolution of http://inspirehep.net/record/926025/plots#0
of the COMPASS result in http://arxiv.org/abs/arXiv:1109.0272 . I would like to see something like http://inspirehep.net/record/925924/plots#0 of the COMPASS result in http://arxiv.org/abs/arXiv:1108.6191 with 0.5 MeV bins and a much better resolution.
Moreover the COMPASS diphoton spectrum is cut at much lower energies (about 10 MeV).
Is that possible at CMS?
Regards, Eef

This is quite the fascinating discussion, not so much because of the reported "result" but the back and forth of those involved (and those who would prefer not to be.)

Mr. T - as you read many, many more papers than I do (and that is an understatement), how many would you say are ever retracted? And what is the effect on those involved compared to others who have results which are wrong (or eventually proved clearly in error) but never retract?

Hi AS,

it depends whether we include or not in the category of "papers" preprints that appear on the arxiv but never make it to a scientific refereed journal.

Retracting an arxiv paper has no effect - I don't think anybody notices. But sometimes nobody notices that a paper makes wrong claims, either. There's a lot of them out there.

The situation is different with refereed papers. Retracting one involves publishing a retractatio of sorts in the magazine - I have no examples to refer to; in HEP it would be quite rare. Corrections and amendments are more common.

In general, the careers are not damaged by bad papers; the system only counts some indicators that are blind to negative qualities of papers (say a published result that gets no citations). But I am not an expert...

Cheers,
T.