% Reply to Berkeley Group % Version 2.0 Feb. 15, 2001 > Berkeley Group Comments on the Draft PRD, "Searches for New Physics > > with a Photon and b-quark Jet at CDF" > > > > We congratulate the authors on bringing this work to draft > publication stage. However, we have some reservations about the paper > as currently written. Our comments follow. > > Jeremy, for Berkeley group. > > General Comment. > > 1. We discussed the "model-independent limits" part of the paper. > Some points that arose were as follows: > > (a) Should general discussion of model-independent limits, and of > how to apply such limits, be in a separate paper, perhaps for > publication in NIM? If CDF is making a contribution to the field in > this matter, the contribution should be evident, and should not be > tied to one particular search. We note, for example, that the title > of the paper gives no clue of this discussion. An alert reader has to > read down to the last sentence of the Abstract to get a hint that > such discussion is present. In a separate NIM paper one could think > of presenting extensive information on the efficiencies of "standard" > (have to be careful with that word) selections in CDF run 1 analyses. > Or, such a paper could describe a "public Monte Carlo" that any > interested physicist could make use of. We really don't think this would be appropriate for NIM. Moreover, a separate paper would have to refer to most of the details of this one,and so would be very ungainly. Having the specific case to refer to when discussion the more general strategy is necessary to keep the discussion grounded. Also we realized that if it were to be separated, we would have to review most of the data and models discussion in order to present the appendix. > (b) Is in fact any appreciable contribution to the subject of model- > independent limits being made in this paper? A cynical reader might > assert: "all CDF has done is give limits in the case of 100% acceptance* > efficiency, and state that any modellers must determine the appropriate > acceptance*efficiency for their particular models". While there are > responses to such a cynic, such cynicism may be encouraged by some of > the wording in the draft, for example the words "A new paradigm... for > reporting results...". While the idea has its downsides, we can also be plenty cynical about the current situation. The idea may not be immediately appreciated but we as a community need to start raising awareness and promoting discussion and this really won't happen until it is down in print. The purpose is more to raise the issue than present a final plan. (New ideas are constantly evolving.) In fact D0 has leap-frogged us in this area with their papers on Sleuth, which is a specific signature-based method that can well be described as a 'new paradigm'. > (c) Some reference must be made to other work concerning > model-independence. In particular, there is the D0 work, "Search > for New Physics....: A Quasi-Model_Independent Search Strategy for > New Physics", hep-ex/0006001 (9 Jun 2000). While "Search Strategy" > is not identical to "Search Results", there are overlaps between > the D0 work and the present work. We have added the references to Sleuth. Perhaps the first paper to address this idea explicity in the modern era is Dave Toback's CDF diphoton search, in collaboration with us. He went on to work on Sleuth with his D0 colleagues to expand on his work at Chicago. Sleuth came out after our draft was written (D0 seems to be able to move in new directions more quickly than we can). > (d) The second para. of Sect. 6 states that "These limits..... do not > have an immediate interpretation." We disagree with that statement. > A limit on (sigma*BR*Aeps) clearly gives a lower bound on the limit on > (sigma*BR) for all models. Any model that predicts a value for (sigma*BR) > that is less than this lower bound will not be excluded by this CDF result. > There is no need for an advocate of such a model to estimate the model's > A*eps value in order to check compatibility. We have added this point. > (e) The inclusion of a "typical" uncertainty on A*eps in the model- > independent limits (2nd para of Sect. 6.1) is at best confusing, and > should be removed. Because (i) the equality given in each of the two > preceding paras., i.e., the (sigma*BR*A*eps)_lim = N_lim/L, is destroyed, Conceptually it's in the definition of N_lim, but we agree we don't say it. We added that text. > (ii) a particular method of combining a statistical uncertainty with a > systematic uncertainty is forced upon a potential user, In all cases we have intended to report N, bg, bg_uncertainties, eff, eff_uncertainty, lum, lum_uncertainty to allow any statistical computation. > (iii) it is not > clear (will not be clear to many readers) that a "typical" uncertainty on > A*eps is always appropriate, All the better to suggest it then since in the majority of cases it is reasonable. (iv) it is better to tell potential users > that a "typical" uncertainty on A*eps is 22%, and let users choose to > accept that or to determine their own value, and to combine it as they > wish. We agree it is best to give the reader all the information to allow alternate computations but we also feel that it is helpful to report what we judge to be the most useful computation. >Point (ii) also applies to the luminosity uncertainty, but the > relative smallness makes the point not so important; however, if the > luminosity uncertainty is included in the limit it would be better to write > the defining equations as (sigma*BR*A*eps)_lim = (N/L)_lim . > If you allow us to include the uncertainty in eps into N_lim, can we also include the uncertainty in L into N_lim? We think this keeps the notation a little cleaner - we have added text explaining this. > (f) The first page of the Appendix is very confusing. > First, just what is being advocated here? Apparently, that limits for > specific model(s) should NOT be given - see the "are [no] longer given..." > in para. below point 6 page 35. That is contrary to what the present paper > does, and we believe many physicists would strongly disagree. That is, > many physicists would argue strongly for giving limits on models that are > of current interest - that is what many CDF papers do. It should be obvious that this way is an alternative to giving limits, if only because we do in the paper. It may be confusing to some for whom these ideas are new, but they are catching on (both talks on Tevatron limits at SUSY2000, one from CDF and one from D0, discussed these ideas- in both cases the ideas originated here). For a more detailed comparison of the merits, see the 1998 Cargese lectures of HJF at http://hep.uchicago.edu/~frisch, published by Klewer or the talk by Ray at http://www-cdf.fnal.gov/internal/physics/exotic/minutes/000519/minutes.html > Second, all the six points given as "advantages" can be questioned. > For example, point 6. appears to advocate that experimentalists ignore > all models. Point 5. appears to be estimating roughly equal likelihoods > of a discovery from concentrating on a particular model and from looking > at variations on a signature, and therefore preferring the latter? Reference [3] has a discussion of the advantages and disadvantages of the two approaches, including a table. These issues are also discussed in the big review article of Reference [19]. To see the problems of current practice, please try to compare the D0 and CDf squark-gluino limits, for example. You will find different values of tan beta, and no way to compare. In addition, D0 turns on all decay channels, and CDF doesn't. These papers are severely compromised by the use of specific models. All we're advocating is a more general approach as an alternative (to complement the other, obviously). > Third, disadvantages to the approach are not mentioned. Such as the > difficulty of how to optimize a model-independent search. Maybe also the > difficulty in ignoring models one knows about when choosing what cut to > make in order to give "model-independent" limits. The addition of the references to the D0 work will help this a lot- these issues are addressed quantitatively there. These are large issues, and we do not pretend to have answers to all the hard questions. However we note that most optimization is done with a handful of variations. For example, this analsis as optimizated with about 10 variations, in the future we hope to attempt procedures such as reporting the results of all 10 points with backgrounds. Another point is that the observation of the pile-up at low delta-phi would have been observed with no model. > (g) The second para. of Section 5 is hard to understand. > We do not know what a "rather obscure" model is, and suspect many readers > will similarly not know. This model is obscure because it is a single special point in the phase space of 335 parameters. Even the original papers (which are referenced) point out that this is a special point. It has been described as being `unlikely' as it requires the chi_1 to be orthogonal to the chi_2 (the first is photino, the second higgsino), so that the photonic decay proceeds by a loop. `Unlikely' is in fact how we have heard it described in several talks by theorists. > We do not understand what "the odds that any of them is the correct > picture of nature are small" is intended to communicate. It's intended to communicate that there are over 300 parameters in susy, and the a priori chance that mu=-400, a_0=0, etc. is small. All SUSY models have the same problem. For example, as recently as Dec 1 at FNAL Tao Han made this very point using the same language we use here. > In the first sentence, in the "choosing models" and "specific models", > does "models" refer to supersymmetry models or to models in general? > Since the models chosen here are all supersymmetry models, presumably > the argument just applies to supersymmetry models, since there are no > words on how any or all other models are like supersymmetry in this > property. Then, is the argument for signature-based limits just for the > case of supersymmetry models? No, why should this be? It seems as if you're missing the key point. We do not know what the new physics will look like- hence we test the standard model, rather than some tiny part of the (huge!!) parameter space of unknown physics. Supersymmetry is a subspace in this parameter space, with dimension of over 300. If one is testing a model that is tight, in the sense that it is highly predictive (i.e. few parameters), it makes sense to test it directly. If one is testing a model that has many degrees of freedom, it makes sense (to us) to advocate as an alternative that one tests the standard model predictions. In general, "what might be discovered next at the Tevatron" is a model with many parameters. > In the last sentence of the para. there are the words "to demonstrate the > effectiveness of signature-based limits". But it is hard find where > such effectiveness is demonstrated. What follows (Sects 5 and 6) are > determinations of the specific model limits and the signature-based > limits, but no obvious demonstration of why one is more effective than > the other. Sentence was left over from other versions - removed. Thanks. > Still more on the last sentence of the para. Sentence clearly implies that > in themselves these SUSY limits are not of much interest. So that the > pages of Sect 5, including 6 Tables and 4 Figs., are not of much > interest. Then why include all that material? Because the two methods do in fact complement each other, as we make clear by including them. It is not a case of either-or: one wants to be able to use both methods, being judicious in the application based on the case. We include these limits because we have the information and the models were topical. They are also the basis of the comparisons in the appendix. > Detailed Comments. > > 2. First line of Abstract: here and in several places in the text, there > is an unusual use of the word "search", which we believe many readers > will find disconcerting. Usually we "search *for* something in some place" > - as for a needle in a haystack. We would rephrase all such unusual uses > of search. In this sentence, maybe "We have searched for evidence of > physics beyond the standard model in a sample of p.pbar collision events > that produce an energetic photon and an energetic b-quark jet." Then a > sentence on CDF and 85 pb-1. We have changed this sentence > 3. First para of Introduction. The Tevatron Collider is a machine and > does not have responsibilities. Perhaps the Director of Fermilab has > responsibilities, but we should not discuss that in a PRD. Fixed. > 4. Intro, para 2. Should be "New physics models often involve...". Fixed. > 5. Sect 2 Intro. Is this para. needed at all? The 85 pb-1 and 1.8 TeV > belong in the Introduction section. And the rest of the para. potentially > confuses by using such wordings as "*the* electromagnetic cluster", > "*the* photon", "'standard'", "standard", "similar ... except..". Many readers (e.g. theorists) will benefit from a brief overview of the data selection, and will not want to go into detail. The introduction (section 1) is more general- we believe that the integrated luminosity and energy are appropriate for a section called 'data selection'. > 6. Sect 2.4. We suspect that some readers will recall that in many CDF top > analyses a SVX b-tagged jet Et cut of 15 GeV (raw Et) was used. So maybe > a reason for this 30 GeV choice should be given. We would also like to know, > since the fake tag rate is low with the 15 GeV cut. SECVTX and, more importantly, its background matrices do not go below 15 GeV uncorrected. We made an early decision to cut on corrected energy since it more closely reflects the underlying quark energy which will be simpler to deal with in the SBS investigations which place cuts on generator quantities. This also relieves theorists from understanding jet energy mismeasurments, at least to first order. 30 is the lowest energy where a raw 15 cut is completely efficient. SECVTX backgrounds are done with the raw energy as normal. > 7. Sect 3.3. Most or all of this para. should be omitted. There is no > need to semi-explain a background method that is not used. It is impolitic > to say "a more sophisticated.." and imply that the top analysis > background estimate was unsophisticated. Besides, there are several top > analyses, some currently in draft status, and there have been changes > over time. It is used later for some background projects, the background shape, for example. We changed "sophisticated" to "complex". > 8. Sect 3.4, 1st para last line. "unmeasured effects" needs some > explanation. We have fixed this. > 9. Sect 3.6, The second para here strongly suggests that the 197 number, > rather than whatever produced the 312, should be used for estimating > the fake tag background. Is there an argument against that? Provided the discrepancy is due to real physics effects, it might be the ultimately better thing to do - it would be essentially saying that we re-measured the tagging background matrix in the photon data. The bottom line though is that it does not change any results significantly (1040+-72+-172 -> 1000+-72+-172) so we don't feel the additional (and substantial!) work is justified. > It should be checked that what is said here (and anywhere else in this > paper) does not contradict the top cross section draft PRD - see sect X > of the July 20 draft of cdf5375. It is hard to compare since he is using different techniques and very different cuts on the photon sample. We completed and blessed this analysis years ago, before his cross section techniques were developed. To use his methods would essentially send us back to square one, with little effect especially since none of the limits on the model would change at all (the background is not subtracted there). On the point of whether the photon negative tags agree with the prediction, from table XIX he sees a low-statistics 27% discrepancy (consistent with zero) while ours is 37% with 7 times the statistics. > 10. Sect 4, para 3 and Fig 1 and 2 caption: The word "approximate" in > "approximate background prediction" seems strange. We have a *background > prediction* . Or perhaps a *background estimate* . Most (possibly all) > such predictions/estimates have uncertainties and so are "approximate". > Can we just call it a background prediction/estimate and explain some > particular approximations that were made. Fixed. > 11. Sect 4 para 4. This whole paragraph should be omitted or rewritten. > First, almost any (maybe any) distribution that has a "tail" can be said to > have several events in the tail. One takes a distribution where one can go > far enough to the right (conventional "european" figure) so that there are > no events further to the right, moves to the left until several events are > to one's right, decrees that one is "at the start of the tail" and by > construction several events are in the tail. Second, where new physics is > likely to first appear is model or guess dependent; historically, the omega > meson and the J/psi meson did not appear in a tail (unless one plotted > 1/abs[m-m0]), for example. Third, whether "a few events at the kinematic > limit" warrant much interest depends on how many "a few" is and what the > background prediction is. I think we are talking about different levels of interest. We meant interesting enough to look at the events in a little more detail, as opposed to interesting enough to declare the events as some kind of potential new physics worthy of investigation of theorists, for example, which is, as you point out, unwarranted (and we state in the paper). We feel readers might have a passing interest in tail events, as we did, so we include a few details. (It's fun to think what it would have been like to do the diphoton analysis and casually look at the events on the Met tail only to stumble across the you-know-what.) Just to keep the history straight, however, the J/psi DID first appear in a tail- in an overflow bin in the wide-band photon beam experiment at Fermilab. If the 6 events in that bin had been looked at, it would have been seen that they all were in a very narrow peak at 3.14 GeV, with no events above and no events below down for a long ways. The history is in fact the other way in most cases- the discovery of the muon, for example, or the discovery of strangeness. The omega-minus and W and Z are in fact rather atypical over the long history of physics (e.g., take sun-spots). > 12. Fig 2, delta-phi plots. Why does the scale go to 360 rather than 180, > and why is there a sharp change at 360 in both plots? Comment-induced bugs - these were originally in radians, changed to degrees (should have been 180) etc. Fixed. Thanks. > 13. Sect 4.1, para 2. Presumably we have consciously/deliberately chosen to > accept two-track tags, so we cannot use a two-track tag to imply that a tag > is not a b. The Pt of 2 and 60 GeV looks like a "discovered-after-the-fact" > additional cut idea, so the discussion "is allowed", but it may be > better if the "unlikely" assertion could be quantified. These events are not cut- they are included in the signal (not sure from this comment if you realized that). This paragraph is a discussion of those events, and is there for the benefit of the reader. The fact that it is two-track does imply that it is in the subsample of tags with significantly lower signal-to-noise. We can look at CDF 2568, Fig 4 and try to do some scaling to see that it looks unlikely but I can't be certain I can show how unlikely it is to have these Pt's. Nonetheless we prefer to leave it in. > 14. Sect 4.1 para 4, does "these" mean "these two" or "these six"? Also, > an extra "not". 'these two' Fixed. > 15. Sect 4.2, On reasons for looking at invariant masses, we should at > least be aware that D0, in their Quasi-Model-Independent Search Strategy > paper, argue (in their Appendix A) that invariant masses are "remarkably > ineffective" in a general search. The J/psi is one counter example; the W and Z are two more. The top was discovered by a search in invariant mass, as was the bottom. In terms of exotics, we have Jacobian peaks in SUSY (and SUSY decays to Higgs and RPV decay peaks) not to mention things like Techniparticles where we are much more sensitive via peaks. So the only thing we can think of to explain the Sleuth comment is that they are saying the sensitivity is less than high-Et counting, which might be true, but not obvious. We know they purposely limited the number of search variables to limit their trials factor. > 16. Sect 4.2 para 3: Text says the small box is as close to the five > events as possible, but that is not the box that appears in Fig. 3. That > is, the small box in the Fig could be appreciably smaller and still enclose > the five events. It is important to note that events cannot be above the diagonal in the small box (actually slightly below the diagonal-- follow the low-mass line) so the true area is triangular. Given that observation, the only way to reduce the small box is to move the left edge from 350 to 440. However due to the above effect, this really only removes a small triangle of area 10 x 20GeV. We could also move the bottom up 10 GeV admittedly, so we have deleted "as possible". > 17. Sect 4.2 and Fig. 5. Text says the min. prob. occurs for a cut at 350 > Gev, but Fig shows 400 GeV . Also in the upper fig the data curve should > be purely horizontal and vertical lines, but is not. Also, the data curve > is .01 at around 450 GeV, while the extreme event in Table 5 is at > 467 GeV. Also, it would be good to assure readers (and us) that in the > pseudo-expt. procedure the statistical and systematic uncertainties on > the background prediction were taken into account. 400 is correct, the 350 was stale text from a earlier analysis. The figure is fixed. Thanks. > 18. Sect 4.3. Some explanation must be given of why the expected > numbers in Table 8 are sometimes negative. And the vertical axis in fig 6 > needs to be adjusted (i.e., go below zero) so that the predictions > can be clearly seen. We have added text to explain this. We have not changed the figure, however; we think it's clearer this way. We have also improved the caption. > 19. Sect 6 intro. Text says "We make an important distinction between the > acceptance ....... and the efficiency." But we see no explanation of why > the distinction is important, nor of what the distinction is. As just one > example, does the tagged jet Et cut belong to acceptance or efficiency, > and why does it matter? > Also, epsilon is the probability of *not* losing events... We have added text. The acceptance can, be computed with only the MC generator, but the efficiency requires the full detector simulation and control data sets. Theorists can do the former but not the latter.