>From FRASCATI@axcdfq.fnal.gov Sun Nov 26 11:04:53 2000 >Date: Wed, 18 Oct 2000 14:08:47 -0500 >From: FRASCATI@axcdfq.fnal.gov >To: velev@fnal.gov, v0565@fnal.gov, rebcdf@fnal.gov, frisch@fnal.gov, > rlc@fnal.gov, frascati@axcdfq.fnal.gov, goshaw@fnal.gov, bed@fnal.gov >Subject: comments on cdf 5450 > > >Dear Authors and GP's, > >I've read the "no new physics" PRD, CDF5450. It's greatly to the >authors' credit that they went from evidence for >new physics to no evidence and just limits. However, >the paper still needs a lot of editorial work, and contains >unexpected prickly surprises in many places. > >In sections 2 and 3, the reader is bombarded with a lot of generic >information, but the basic facts and numbers are missing. >It is a long paper, and still has less useful details than a PRL. As examples: >1) there is no mention of how many photon +jet events we select The last sentence of section 2.3 says 'these requirements yield a data sample of 511,335 events in 85 pb-1 of exposure. The number of events after tagging are given in the last sentence of the 1st paragraph of 2.4, and, after an Et cut, in the last sentence of the 2nd paragraph. However we are willing to add a table if the gp's think it is an improvement. >2) the b-tagger is referenced as JETVTX, but I believe it is SECVTX. > It is mentioned its usage in the top discovery; however, is it > really the same tagger ? We don't find the word JETVTX in the text. The reference for the tagger is the top discovery paper which used SECVTX which is the same code used today. > Do we know that this time it is used correctly ? It was not used > correctly at the time of the evidence for new physics (CDFNEWS 10131). Yes, it was used correctly. >3) mistags - it is not clear how they are calculated (the reference is outdated). > Actually, mistags are approximated with negative tags, which is not correct. > It is not clear which parametrization of the negative tags is used. > In section 3.1 is mentioned that the sample has 197 negative and > 312 predicted (how?). Using the standard methods as indicated in the references cited. > The top cross section PRD shows that CDF predicts correctly the rate of negative > tags in the photon sample. Can one explain how it is possible ? From table XIX there is a low-statistics 27% discrepancy (consistent with zero) while ours is 37% with 7 times the statistics. We would like to investigate this, in fact update several things, but there is simply not enough time to reduce the systematic uncertainties on a background calculation that is not used in setting limits and is covered by the systematic uncertainty. >5) W/gamma and Z/gamma backgrounds are negligible, but it should be > explained in more detail how they are evaluated We rewrote the sentence to make it more clear. >6) it is surprising that there are tagged photons. To say that they are removed > is does not seem good enough As we recall, when we looked more closely at this years ago, we found the requirements of tagging and tracking isolation allows a small probability for a photon to be tagged, simply as background. This occured with only one photon in the whole sample so it is a negligible effect. >7) no mention of QFL, and its problems, as track degradation or tagging > efficiency scale factors. What is it done exactly in this analysis ? We ran the Monte Carlos using a talk-to similar to the original top cross section analysis. This was recently checked against the current best methods from 4939. Since no tracking degradation was applied, we used the original scale factor of 1.06, approximated as one. In all the discussions of scale factors etc, it is important to keep in mind that the background is not used to set model limits, and only one limit on one minor model is actually achieved. To demand the precision of the final top cross section analysis is simply not a good use of resources. Discrepancies are covered by the 20% systematics. >8) the evaluation of the rate of fake photons should be supported by plots to convince > the average CDF collaborator first, and then the average reader. > After all, this analysis does not use > the standard CDF definition of isolated photon. The low-Et photon has box isolation instead of cone isolation. This was done to have a slightly tighter requirement than the trigger in order to avoid measuring the trigger efficiency. Since photon backgrounds were derived using events collected with a similar trigger, those events have a similar requirement. Bob Blair recalls the second CES cluster is different but was verified at that time to have a negligable effect on the background estimate. > Now, a more substancial point; the background is evaluated using the equivalent > of Method II for W+jet events. > However, here one uses a simulation of gamma+heavy flavor which > is not documented. This is especially bad because the calculation is done by one > of the paper's authors. > The matrix element has been published ? The implementation of it into a > simulation is public ? Who checked it in the collaboration ? We quote Michelangelo's answers to this: `Yes, it was done and published several years ago by Kunszt and Ellis, and by K.Ellis and Nason: %\cite{Ellis:1988qy} \bibitem{Ellis:1988qy} R.~K.~Ellis and Z.~Kunszt, %``Photoproduction And Electroproduction Of Heavy Flavors With Gluon Bremsstrahlung,'' Nucl.\ Phys.\ {\bf B303} (1988) 653. %%CITATION = NUPHA,B303,653;%% %\cite{Ellis:1989sb} \bibitem{Ellis:1989sb} R.~K.~Ellis and P.~Nason, %``QCD Radiative Corrections To The Photoproduction Of Heavy Quarks,'' Nucl.\ Phys.\ {\bf B312} (1989) 551. %%CITATION = NUPHA,B312,551;%%' > The implementation of it into a > simulation is public ? Again, from MLM: "there is not much more in the simulation than the matrix element MC itself, based on the available matrix elements calculated for photoproduciton in the above references. I don't recollect having given you a version with the herwig interface (I don't have it in my files, at least, but it may have been buried in my obsolete fnald account) So there isn't really much to check, once I checked that the matrix element code gives the right parton level results." He did install it in HERWIG for us, but we don't know if this is public. > Who checked it in the collaboration ? MLM: `Nobody, to my knowledge.' > In addition the systematic error of the calculation has to be determined correctly > and not by handwaving; scaling Q^2 by a factor two is arbitrary. An error of 30% on > the Mangano calculation is also arbitrary; for example, this is the error he estimates > on its calculation of the bbar production cross section, but the calculation > is different from the data by more than a factor of two. > I am surprised that the quark mass makes a 10% difference for jet with E_T > larger than 30 GeV; ABSOLUTELY SURE ? The 10% was how much we varied the b mass and the resulting cross section changed by 10%. The Q**2 and quark mass uncertainties were not propagated into the efficiency. > Finally, one should not add a 20% error for unmeasured effects; why > 20%, anyway ? MLM wrote several years ago: "I would then find something like 4.8+-1.5 , i.e. a +-30% uncertainty. Using the mbb instead of pt gives values pretty much witin this range. So I guess that +-30% around the predictions obtained using mb=4.75 and the default choice mu=pt is reasonable. Use +-50% if you want to be on the safe side, mentioning however that the estimated scale dependence is only +-30%. The additional 20% could therefore account for additional effects which cannot be determined by simply changing the scale dependence. " MLM replies today: "I don't think we need to explain more about these "additional effects", provided you use the sentence I suggested in my letter: "... which cannot be determined by simply changing the scale dependence." It simply states the fact that varying the scale is a way of assessing the potential error induced by the lack of higher order corrections, but is no substitute for a full NLO calculation. " We had rephrased his sentence, so will go back to quoting him. > Actually, I believe that the focus of the paper should be just on > measuring the production cross section of gamma+ heavy flavor. > However, if one insists in putting limits to supersymmetric > particles, then one should use another sample (like conversion > gammas with E_T > 10 GeV + jets) to calibrate the simulated gamma + > heavy flavor production. Without this work, Sections 4 and higher > are worthless since they rest on an unchecked calculation with an > unknown error. The limits on the models are set assuming the 2 observed events are signal, there is no background subtraction for the models limits. The background should be considered a consistencey check. > As a detail, the background shown in Figures 1 and 2 is not calculated according to > Table 3, and the justification for this in pg. 9 is at least not very clear. We tried to state it clearly. The background total is estimated by the photon background methods. If this method were applied bin-by-bin, the uncertainties on the low statistics in each bin would be enormous. > > I do not understand the reason of singling out events > with large missing E_T by run and event number > since they are perfectly consistent with the background. Section 4.1 > should be dropped. Since it is unlikely we can predict the way that SUSY will appear in the data, it is important to check for anomalies where we can. To investigate the events on the tails of missing Et would seem natural. in particular we have to ask if they are not only on the tail of met, but extrodinary in some other way that does not automaticaly fall out of the analysis (such has containing a second photon), or if they all look particularly similar to each other, with the same dijet masses, for example. > The five events with a large di-jet mass could potentially be more interesting; > however, the background calculation is not accurate and, because of this, > I see no point in singling out 5 events in Section 4.2. The events seems to cluster apart from the the other events so it is natural to ask if the separation is significant, even if the significance is hard to be precise about. The accuracy of the background is less than ideal but we think the uncertaintes are reasonable. We hope it is more usuful to include the estimate as we can reasonably do it, rather than give up on trying. > Section 4.3 lists the number of events as a function of the jet-multiplicity, > where the additional jets have corrected E_T larger than 10 GeV. > Can we show that we can model the data in some other sample ? if not, what is > the value of this Section ? Does the Michelangelo calculation predict the jet > multiplicity for gamma+ heavy flavor ? > As a detail, why some ecpected number in Table 8 are negative ? > The higher jet multiplicities would be predicted by the standard Herwig; they were not specifically checked. The negative predictions are from the large fluctuations in the photon background subtraction. Effectively it means, for example, the number of events with a CPR hit is greater than the number predicted for a sample of pure background. > In section 4.3 what is the point of mentioning the number of double tags, if we do not > know the background ? Without a background, we can't claim whether a signal exists but it is still descriptive of the sample and could be used to set limits assuming the events were all signal. > In the same section, what is the purpose of Table 9 ? We are reporting the observation of an interesting event. > > As said before, Section 5 does not serve any purpose if we don't have a > defensible background estimate. > > Section 6; I do not understand what we gain in this section with respect to > the pure list of the rate of observed events. > The acceptance may be ease to be evaluated by model builders, epsilon not > for sure. > At least, > the title of the section is not > correct: it is a limit on cross section times detector acceptance. We removed the "cross section" from section 6.1. > > Why the uncertainty on the luminosity is quoted to be 8% in Section 6.1 ? Beacause this analysis was blessed when that was the official uncertainty in the luminosity. We have changed this to 4%. > > Why Section 8 has to be in a CDF publication ? It could easily > be a rapid communication of the people who did this work. There are several options for publication, making it an appendix clearly sets it apart from the central results. > I was puzzled that in Section 8.1 one efficiency is quoted as a > private communication of one of the > author of the paper. We removed it. > regards, Paolo Giromini > > ps: I could not find any comment on the web (where are they ? ) Thanks for the comments. The URL for the comments is: http://hep.uchicago.edu/cdf/rlc/prd/prd.html