[Clascomment] OPT-IN: Comment on the narrow baryon peak reported by Amaryan et al.

[Gabriel Niculescu]

Dear all-
I read and opted-in on this paper mainly because I agree with its intentions. The format, as others have noted is less than optimal: we sound bitter, occasionally vengeful, and some of the arguments used are weak (see the discussion about "their background" vs "our background" others have mentioned). 

We keep getting back to the process through which the analysis (and its results) were voted down by the collaboration. The process through which analyses/results are approved by CLAS is of course important, but that is an internal matter for the CLAS/Hall B/JLab, not for an outside reviewer or reader.

Furthermore, the CLAS review/approval process is meaningful as long as the members abide by it - which is clearly not the case for Amaryan et al. paper. The fact that we insist of retelling the story of this paper failing to get CLAS approval is not helping at all as the authors of the paper we comment on chose to IGNORE and BYPASS that vote.

Personally I think that on this matter we should take the high road and bypass any individual likes (and dislikes) and combat the Amaryan et al. paper based on its (de)merits, of which there are many (sorry if I reiterate points other collaborators have made already):

- In order to justify the cuts applied the paper only quotes a momentum resolution for CLAS (a bit on the optimistic side, one would think), nothing for the angular resolution, nothing for the eloss correction, etc. When evaluating 2-3 particle invariant/missing masses, all these corrections will contribute and the size of the cuts should be compared with the resolution one gets in this or that invariant mass. My feeling is that the cuts used are too aggressive.
- I fully agree with Matt's comment that a blind/double blind analysis would have been called for. Matt (and Curtis, Mikhail) had other comments/suggestions that I think need to make their way in this paper.
- The "log-likelyhood" used to "show" that the significance of the peak is 5sigma is flawed: there is no penalty for the larger number of parameters in the peak+background scenario vs the background-only scenario. Also it is not clear over what range the summation in the formulas 3-5 is carried out: 1.45-1.75 or just in the immediate vicinity of the bump? The answer will differ significantly depending on the choice of this region
- The phrase (in the Amaryan et al paper) "It is worth mentioning that when we fit the background with a smooth polynomial function, we obtain even higher statistical significance in the range of 6 − 7 GeV depending on the fit range." in my opinion tells the whole story of the paper and should be attacked as such: 
 * the authors do not have a solid understanding of statistics (or chose to ignore it)
 * if indeed one can use a "smooth fit" and magically increase the statistical significance of the peak from 5 to 7 sigma, why bother with anything else
 * no fitting of the data, be it a smooth polynomial, a scaled (scaling is a form of fitting!) monte carlo shape, whatever, cannot take one away from the simple fact that if one has N events in a region and fits a S+B (S+B=N) over it, the uncertainty on S is of the form sqrt(N+B) (yes, plus!). The only way one can get away from the predicament is by separately calibrating one's instrument in the absence of the signal. 
 * this is getting too long, there are other statements/facts that can (and should) be attacked in refuting the paper in question.

Lastly, my hope would be instead of rushing to submit the comment in its present form  we'll try to incorporate some/most of the good ideas/comments made by fellow collaborators, hopefully producing a much stronger paper that definitely adjudicates this matter in our favor.

Sincerely,
Gabriel Niculescu