Questions from Gustaaf Brooijmanns ******************************************************************************* > -p8, bottom: it would be nice to back up the statement that the double b-tag > eleminates the light quark component of the sample with some rough numbers. > What are the light vs b cross-sections x tagging efficiencies in the range of > interest? A: Some insight can be obtained from Figure 16. (Per, perhaps you could refer to the Figure at the bottom of page 8?) The bb/light fraction is about 1/10 in the single-tag sample. After tagging a second time, this would go to about 0.4/0.1=4, so the light stuff makes up about 25% of the double-tagged sample (this is also in rough agreement with more detailed studies in the bbh(->bb) analysis). > In fact, it would be particularly nice to give the composition of the single > tag sample, since it's the shape of that sample that's used to model the > background. BTW, it's important to show that light QCD and bb QCD has the > same shape in dijet invariant mass: if bb QCD were to drop off faster than > light QCD, the basic principle of the analysis would be bogus. A: Right, see Figure 16. It's difficult to show that the shapes of bb and light are the same, but this follows from symmetry in QCD, once the sqrt(s) of the production >> m_b. this can and has been seen in MC. And the fact that the method works at all is some proof. > -Method 1: A few questions: > Does the vertical scale in fig 5 agree with the measured SVT efficiency in > data when the sample composition is taken into account? P: An average double to single tag rate of 0.07 corresponds to a bb/light fraction of ~0.18. The higher b content is due to the muon trigger used in method 1. I will add information on the sample composition to the text and a reference to fig. 16 as Andy suggests. > There are some pieces of good news: the 1.18 scaling factor in fig 9 seems to > correspond rather well to the average ratios of double tag and singletag > above and below dphi of 3.0 shown in fig 5. I don't understand how is comes > about that the method illustrated in fig 10 is apparently overestimating the > background, such that you need to scale it down by 0.96. Does anybody > understand why this is? Shouldn't it be "just right"? This normalization > factor, BTW, corresponds to 588 events below 120 GeV,scarily close to the > excess of 731+-200 events. P: As mentioned in the text, one can actually obtain the normalization in fig. 9 from a fit to the tag rate vs. dphi in fig. 5. This was done in an earlier version of the analysis. The problem is that it results in a larger uncertainty on the normalization factor. The method in fig.10 should by construction produce a background template with an _identical_ number of events as the observed double tagged events integrated over the full mass range. The normalization factor would be identical to 1 only if the relative distribution of events above and below 120 GeV were identical in the observed double tagged events and the background template. The deviation from 1 is due to the difference in the invariant mass shape between the estimated background and the observed double tagged data. We have more double tagged events in the low mass region around the Z mass. Applying the normalization factor to the background gives rise to exactly the observed excess in table 12. The critical factor is the _error_ on the normalization factor (not the normalization factor itself). From the fit error (fig. 10) this is taken as a 1.5% uncertainty on the absolute number of background events. > In fact, looking at table 12, it seems that even after the normalization > factor the shape of the distribution may not be reproduced that well above > 120 GeV. It starts by fluctuating high (at a point where signal contribution > is already small), then dips under the observed curve. These two effects > combined don't make me fell all warm and fuzzy: if the shape isn't > understood, the subtraction method is no good. P: The shape of the background distribution was fitted to the observed shape of the data above 120 GeV as part of the normalization. This is the only region where we can test the shape with no Z contribution. The result of this fit is displayed in fig. 10. It reveals no discrepancies outside the errors in _this_ mass region. The chi^2/ndf is good. > For this method I really think it's crucial to document the sample > composition much better, and illustrate the behavior of trigger and > recoefficiencies in the turn-on zone in extreme detail, to show that the > potential shape difference suggested in table 12 is indeed statistical in > nature. As you say, the difficulty is to understand the QCD bb background, > but while there's a focus on quantification, there's littleinfo on shape > issues. P: To demonstrate the absence of significant light vs. b quark differences from the combined trigger, reco and analysis efficiencies below 120 GeV, is extremely difficult - see Andy's comments above. The fact that the excess peaks at the Z peak, agrees with expected signal rate and signal dphi distributon is encouraging, but does not exclude that there are other effects due to b and light quark differences contributing to the excess. Such effects have not been treated or discussed in method 1, other than the agreement at higher masses in fig.10. One way forward towards estimating light vs. b quark biases in the analysis would be to make detailed MC comparisons of bb and light quark QCD events passed through the trigger and analysis chain. This would require large MC statistics of low pT QCD with muons (due to the skim/trigger). The necessary MC samples for this, however, do not exist. Data/MC agreement would of course also be an issue. Another approach is to perform a similar check to that in section 7 and _measure_ the effective invariant mass difference between an un-tagged (light quark dominated) and single tagged (b contaminated) real data sample and derive a correction for the light vs. b quark invariant mass shape bias. From the analysis in section 7 it is seen that the net effect of such a correction in the 60-100 GeV mass window amounts to ~70 events, or 1.0% of the number of background events. This is smaller than the error on the normalization factor, but not negligible and this contribution _should_ be included in the error in method 1. I am currently running over the exact sample used in method 1 to measure the effect of such a light to b-quark correction on this sample. > -Method 2: it's very difficult to say something sensible about this sinceI > have no idea what is meant by "A TRF is derived on the un- tagged sample and > re-applied to the same un-tagged data sample". How is this TRF determined? > How accurate is it? How big is the determined fake rate? Clearly the same > thing applies to determining the TRF from the single-tag sample and > reapplying it to that sample. A: Yeah, it's done in exactly the same way as for the TRF from the single-tag sample. The TRF is by definition perfectly accurate. The tag rate (I assume that's what you meant) is slightly smaller than that from the single-tag data, since there's less heavy flavor in the sample. > In figs 21 and 22 we don't know which is which, and the description of fig 20 > in the text (top p26) isn't exactly what fig 20 actually is. A: The green is corrected for the Z->bb in the 1-tag sample... it's labeled on Figure 22... Per, could we add that to the Figure captions? Thanks. Per, the top of page 26 should say, "This scaled signal peak is then divided (bin by bin) by the single-tag data, to determine the estimated fraction of Z->bb events in each bin of the single-tag data, as shown in Figure 20." P: I will modify the text and caption. Questions from Frank Filthaut ******************************************************************************* - there is a statement somewhere in the beginning of the note that it focuses primarily on the pre-v13 dataset. However, from the results I conclude that the v13 data have not been used at all. Is this correct? Even though the v13 sample is substantially smaller than the pre-v13 one, is that enough reason to discard it completely? Andy: The v13 data was not included in the PASS1 data set, so I could not use it for the PASS1 analysis. Per's reason was that the triggers were totally different, thus the turn on curves were different and he was concerned that the shapes of the data could not be reliably combined. Per: The v13 data was not used for the results. In addition to the turn-ons, the tag rate from the v13 triggers are significantly different from the pre-v13 data due to the impact parameter filters at level-3. The v13 background estimation will therefore have to be treated separately from the rest of the data. Due to the much lower v13 statistics it will have larger uncertainties and in combination with the lower signal yield (table 10), it was found not worthwhile to include this data in the current analysis. It will wait for the 1 fb-1 p17 analysis. - the parametrisation of the TRF in three bins of |eta| seems somewhat coarse. Has an attempt been made to make an alternative parametrisation that assumes factorisation between the jet |eta| and ET dependence, as has been done for the last certification round in the b-ID group? Andy: You are right that the number of |eta| bins should be varied (from 1 to 10, for instance) and the difference in the resulting peaks should be taken as a systematic. We did not do this for this preliminary result. The PASS2 bbh(->bb) analysis has tested both 1, 3, and 5 bins... and we saw little difference between the resulting background predictions from 3 and 5. - the search for Z -> bb, to my mind, always had as one of its primary goals to improve our knowledge on the b-jet energy scale. In that sense, I find the choice that is made in Sect. 6.4 (p17), namely to drop from consideration the background estimate obtained using the "out-of-zone" TRFs, somewhat worrisome. Moreover, the method described in Sect. 7 finds yet a different mass (79 GeV), without there being a discussion of this difference. Finally, in both methods it is said that the peak in data agrees with that in MC, but that necessarily implies that the same MC(?) displays a different peak in the two methods. I'd like to understand that... Andy: I don't see why not using the "out-of-zone" TRFs prevents us from improving our knowledge of the b-jet energy scale. Are you concerned that we are only measuring the b-jet energy scale based on jets with dphi>3.0 and events with njets=2, thus a direct comparison with ttbar events (for example) would be difficult? Yes, the MC samples and the data samples are different! We would be worried if our results did not agree in MC. :) One analysis is PASS1 and the other is PASS2. The PASS1 does not use T42, and also uses a different JES. I also applied the _muon_JES_ corrections, and I'm not sure if Per did. Per, can you add a sentence or two to clarify that they are different samples? Per: The in-zone TRF describes the double-tag in-zone data better at high masses and the normalization correction is smaller. Applying the out-of-zone TRF to the in-zone single-tagged events leads to a 4 GeV shift in the background subtracted mass peak. The fact that there's a shift indicates that there is a dphi dependent mass shape difference between the in-zone and out-zone TRFs (so, in addition to the TRF scale difference, shown in fig. 5). By using the in-zone TRF we are working within the same dphi region and thus eliminate any such bias in the background estimate. Regarding the mass difference between methods 1 and 2: method 1 is pass2 with muon_JES_correction, method 2 is pass1 with muon_JES_correction. I will clarify this in the text. In addition, from MC studies we know that the position of the peak is sensitive to trigger, muon and jet pT selection, which all differ between method 1 and method 2. I will add some discussion to the text. - how were the estimates of the bb content in the untagged and single- tagged samples (p24) made? Given that these events have associated muons already, these estimates seem rather low to me. Andy: The fraction of heavy-flavor in the untagged and single-tagged samples were done using the Pythia bb MC sample (shown in Fig. 16). The bb MC is normalized to the data using double-tagged data and MC events. The assumption is that the double-tagged data is nearly pure bbbar. The PASS1 analysis did not select by trigger or require muons offline. Per: The pass2 analysis with both trigger and muon requirement has about twice the heavy-flavour content after single tags. - I would tend to agree with the argument made (on p23-24, fig. 17) that going from the untagged to the single-tagged sample can shift the distributions due to a difference between b- and light-jet energy scales. However, I fail to see how the comparison with the Z->bb MC (fig. 17) helps to support that argument in any way? Andy: The point of including the Z->bb MC peak in Fig. 17 is just to show the relative magnitude of the correction, and also to show its shape and location relative to the signal shape and location. The conclusion is that the shape of the induced shift is not similar to the signal, and so could not fake the Z->bb peak. - is the binning shown in fig. 18 really what is used to apply TRFs? The statistical uncertainties towards high ET become so high, that it would appear much more reasonable to use wider bins and then smooth the TRFs. (The same question holds for the TRFs displayed in fig. 7, by the way -- it's just that the scale there goes up to 80 GeV only, that is why it does not look so dramatic.) Andy: Yes, this was the binning used to apply the TRFs. The worry about using an interpolated function of some kind, or a larger pT bin, could induce a shift in the predicted background shape, since there are more jets at low pT and thus the jets near the high edge of each bin would always have their tag rate systematically underestimated. Per: Improved binning and fitted TRFs is a good point, which can be studied for the p17 version of the analysis. Questions from Gordon Watts ******************************************************************************* I have two minor questions about this analysis: 1) You add 50 pb-1 with the v13 dataset, which is 1/6 of your total dataset (300 pb-1). Yet the number of Z's goes only from 730?810, or about 80, or 1/10th of the total number. Does this make sense for the various acceptances (I didn't see anything obvious). Per: Neither of the analyses actually used the v13 data for the results. The difference between the numbers found with method 1 and method 2 is instead due to the different corrections and trigger and event selection, see Andy's comment. (The expected number of Z->bb candidates from the v13 sample in method 1 is 87.7 events, see table 10. The lower signal efficiency in v13 vs pre-v13 is due to the tighter trigger requirements needed to keep the triggers un pre-scaled.) Andy: There are numerous differences between the cuts and corrections used in the second analysis. For instance, there is no specific trigger requirement, the dphi cut is looser, the Z->bb in the TRF is corrected for, etc. Therefore, a direct comparison of the number of events is difficult. 2) In figure 22 you have the Z?bb MC plotted. I didn't see anything in the text that describes how you apply the various btagging estimations to the MC. Do you just treat the MC as you do the data when calculating the backgrounds (i.e. apply the TRFs), or is something special done? I may have missed this in the text. Andy: For the second analysis, the Z->bb MC is tagged, just like the data (but the data/MC scale factors are applied, of course). And then the inv. mass of double-tagged events is plotted. There is no background in the MC. Per: The Z->bb MC in method 1 is smeared, b-tagged and scaled with data/MC scale factors and then passed through the event and trigger selection (trigsim) before the invariant mass is plotted.