D. L. Nordstrom Editor Physical Review D Email: prl@aps.org Dear Dr. Nordstrom, we would like to thank the referee for their time, effort and thoughtful reading. In general we find that the comments are clear and show a dedication to upholding both the standards of the journal as well as the standards of the field. To summarize the referee's comments: This paper is both "interesting" and "intriguing" but is unsuited for publication on Phys. Rev. D because of two primary reasons. 1) It fails to meet what they believe are the criteria required for Physical Review papers 2) It is not a carefully done study We believe that both of these assertions are untrue so we have revised our manuscript for their comments and are resubmitting it. In this document we will respond to the referee's criticisms and show why we believe their assertions are not true. We address them one at a time beginning with the primary assertion about publication. The referee also made many criticisms regarding specific issues that need to be addressed before publication. We agree with many of these items and have addressed them one at a time, along with our responses/changes. We hope the editor and referee find our updated draft and responses satisfactory. Please do not hesitate to contact us if there are questions or concerns. ************* 1) It fails to meet the criteria required for Physical Review papers The webpage we found, http://prd.aps.org/info/polprocd.html, that lists the criteria for publication of papers in Phys. Rev. D is quite detailed, but is somewhat ambiguous. We quote two different sections of the referee instructions: "SUBJECT AREAS Physical Review D1 generally covers experimental particle physics and phenomenologically oriented theory of particles and fields. Physical Review D15 covers more formally oriented theory of particles and fields, gravitation, cosmology, and allied areas. (More detailed information follows.) Authors are welcome to indicate an issue preference for papers on borderline subject matter. Physical Review D1 includes papers on subjects such as the following: experimental particle physics (and experiments in other areas of physics whose results are relevant to particles and fields); cosmic-ray physics; phenomenology of collisions; decays, masses, and other properties of particles; electroweak interactions; applications of quantum chromodynamics; development and application of more phenomenological approaches to strong interactions; development and application of specific realistic or semirealistic models beyond the standard model; other theoretical developments of phenomenological interest; lattice gauge theory." It also details a section "Proposed experiments." The reviewer has, in our opinion, incorrectly assigned our paper into this category despite that they realize that "The authors are not proposing a whole new experiment." To re-quote those requirements. "Papers that describe proposed experiments fall into a special category. For such papers to be acceptable, the experiments must be demonstrated to be novel and feasible. It is the authors' responsibility to show that their proposal is likely to stimulate research that might not otherwise be undertaken. Generally not suitable for Physical Review are papers proposing a new experiment using straightforward calculations based on well-known theories or models, and papers describing simulations of apparatus or optimization or feasibility studies. " Stated succinctly, we are NOT proposing an experiment. We are writing a paper which we believe is a phenomenology paper, and could easily be classified (depending on one's definition) in any, if not all, of the above ways. Specifically, as: 1) phenomenology of collisions; 2) development and application of more phenomenological approaches to strong interactions; 3) development and application of specific realistic or semirealistic models beyond the standard model; 4) other theoretical developments of phenomenological interest We certainly sympathize with the reviewer that given the "Proposed Experiments" criteria it would be very difficult to review this paper, and by using those criteria that publication might be inappropriate. However, we believe these are not the appropriate criteria for use in reviewing our manuscript. We, and many of our theoretical and experimental colleagues, were quite surprised to see our paper so narrowly interpreted. The main issue, according to the referee is: > "Is doing a toy MC simulation of a particular hypothetical process, > which MAY > lead to resolvably delayed photons, something that is novel and worthy of > publication in Phys. Rev. D ? My judgement is that it is NOT; it is a > straightforward calculation based simply on kinematics." We disagree with this assessment and judgement. This criteria is clearly not an impediment to publication of the papers that phenomenologists typically write. In our experience phenomenology paper often investigate, 1) with simple Monte Carlo detector simulations, 2) the prospects of hypothetical analyses of known theoretical models such as SUSY or Large Extra Dimensions 3) they propose analyses (not new experiments) at the Tevatron, LEP, LHC or, even the SSC to go back a ways. For the edification of the editor and referee, and to bolster our position that what we describe as a phenomenology paper is a common type of publication in Phys. Rev. D, we have done a literature search for Phys. Rev. D's of similar style that detail the prospects of doing searches. There are LARGE numbers of similar papers. We list a few, many by some of the most prominent theorists/phenomenologists in the high energy physics community, which are similar in style to ours. This list is in no way intended to be complete. They include (trying to sample various theorists over many years): - U. Baur, T. Plehn, D. Rainwater, "Probing The Higgs Self-Coupling At Hadron Colliders Using Rare Decays", Phys.Rev. D69 (2004) 053004, http://arXiv.org/abs/hep-ph/0310056 : - U. Baur, T. Plehn, D. Rainwater, "Determining the Higgs Boson Self Coupling at Hadron Colliders", Phys.Rev. D67 (2003) 033003, http://arXiv.org/abs/hep-ph/0211224 - J. K. Mizukoshi, H. Baer, A. S. Belyaev, X. Tata, "Sneutrino Mass Measurements at e+e- Linear Colliders", Phys.Rev. D64 (2001) 115017, http://arXiv.org/abs/hep-ph/0107216 : - U. Baur, D. Rainwater , "Probing Neutral Gauge Boson Self-interactions in ZZ Production at Hadron Colliders", Phys.Rev. D62 (2000) 113011, http://arXiv.org/abs/hep-ph/0008063 : - H. Baer, C. H. Chen, F. Paige, X. Tata, "Signals for Minimal Supergravity at the CERN Large Hadron Collider: Multi-Jet Plus Missing Energy Channel", Phys.Rev. D52 (1995) 2746, http://arXiv.org/abs/hep-ph/9503271 : - H. Baer, C.H. Chen, C. Kao, X. Tata, "Supersymmetry Reach Of An Upgraded Tevatron Collider", Phys.Rev. D52 (1995) 1565, http://arXiv.org/abs/hep-ph/9504234 : - A. Stange, W. Marciano, S. Willenbrock, "Higgs Bosons at the Fermilab Tevatron", Phys.Rev. D49 (1994) 1354, http://arXiv.org/abs/hep-ph/9309294 : - J. Rosner and L. Stodolsky, "Direct-Photon Searches As Tests For Unconventional High-Energy Electroweak Interactions", Phys.Rev.D40 (1989) 1676 A few more comments are in order before we proceed with the other issues. One can ask if the analyses the papers above suggest are any more likely to be performed than the one we propose; the answer is no (especially for the SSC papers). One can ask whether their methodologies are any more novel than the ones we propose; we point out that in our paper that not only do we investigate the prospects of a novel technique, we describe the technique and, if used, that it would be the first of its kind at the Tevatron for so difficult a search. One can ask if our analysis is feasible. Even the referee believes it feasible. We note that we have used results from run I of the Tevatron and preliminary Run II results to extrapolate to Run II data. This is surely a better estimate of reality than the projections to the LHC or SSC that are routinely published. To be sure, there are remaining experimental details which need to be worked out, but those would require a detector specific full GEANT level simulation and beyond the interest of the reader of Phys. Rev. D. These are surely no more likely to be a problem than the lack of proper background estimation techniques and proper ID efficiencies typically employed in many phenomenological papers. Furthermore, since our technique and prospects are applicable to any detector at a collider machine, each detector would require a separate simulation; again outside the scope of any reasonable phenomenology prospects paper. Again, one could imagine writing a paper on such a study, but that would be more suitable for NIM and not of interest to the general reader of Phys. Rev. D. who wants the type of results we have presented. In other words, we believe it's important to publish the physics prospects and capabilities of new instrumentation and how that could impact on our understanding of the physical world around us. To summarize our answer on this question, we believe that the paper we have written easily fulfills the requirements to be considered as a phenomenology paper for publication in Phys. Rev. D. It should not be subjected to criteria for which is it not designed to fulfill. According to the proper criteria for Phys. Rev. we believe our results are quite substantive and interesting, and should thus be published barring the resolution of specific issues of "correctness" of the study. We address this next. *************** 2) It is not a carefully done study, and there are other issues which need to be resolved. We appreciate the careful work which has gone into the review and we have fixed the paper for many of the referee's criticisms. We thank the referee for pointing out issues of concern and we have fixed the places where the text was insufficiently clear in detailing why this is a careful, thorough and detailed analysis. We next address many of the specific comments individually. We will quote the referee and give our responses. > In addition, to this basic content issue, the paper is currently > rather verbose > and in my opinion, presented at a quite pedestrian level. There are also > several typos etc which I would have expected should have been caught prior to > submission with proper internal review. We agree with that the previous draft was too verbose and have fixed it. Our guess is that the comment about the verbosity and the "pedestrian level" is really directed at Section II which uses a toy MC to show on how timing is used to distinguish long lived particles. While there is nothing novel about toy MC in general, we note that this section was frequently the most interesting to our experimental colleagues who saw drafts of this paper and presentations on this work. In the interests of brevity, but in keeping the useful detail, we have relegated this section to an appendix and shortened the text to be more theory/phenomenology/results centered. We are, frankly, embarrassed by the typos and they have been fixed. We have double checked our results and found no substantive errors. > Last, but not least, I am concerned that other collaborators > particularly those > who have done much of the work related to the CDF EMTiming upgrade have not been > included as co-authors. Ref 2 indicates that there are about 15 people directly > involved in this upgrade project. While we understand the instinct to have all the co-creators of the EMTiming project listed as authors, we disagree with the referee on this issue. This is inappropriate for two reasons, 1) They didn't work on these prospects results in any way so asking them to lend their names in support of work they do not know is inappropriate (again, this is a phenomenology paper, not a proposed experiment paper), 2) No phenomenology paper we have seen which quotes the prospects for CDF, DZero, Atlas, CMS, Aleph, Delphi, Opal, L3, etc has EVER listed all the names of the people who helped build the experiment or designed the particle ID, estimated backgrounds etc. It simply isn't usual and customary. Where we have used someone's work, we have cited them which is our understanding of the right thing to do. We note that all the people who, in the referees opinion, could have been authors have been asked about their feelings on this issue and they concur with us on this issue. > I judge the "proposed experiment" to probably be FEASIBLE, although > the > definitive information which mostly leads me to this is information from a > presentation by Goncharov available at the URL in reference 2 indicating the > timing resolution for electrons. It would be preferable if such information was > directly in the paper - and presumably Goncharov and others who contributed more > to building and commissioning the detector should then be authors. Also by > largely limiting the paper content to the prospects for the photon-timing to > improve the search reach, the authors have not really addressed in much detail, > the actual feasibility of the search as a whole, relying largely on old > publications with a different detector operating in different accelerator > conditions. More details related to this are contained in my "scientifically- > sound ?" comments. Again, if this were a "Proposed Experiment" paper we might agree that more detail on the hardware is appropriate. However, this is a phenomenology paper so such detail is outside the scope of this paper and should be put in an appropriate citation. There are surely experimental issues to be worked out before the analysis can be completed, but this is SURELY true of all the papers listed above as well. We surely agree that an experimental paper should be written on these issues: both on the equipment (presumably in NIM) and when the data has been taken and analyzed (in Physical Review Letters or D). It is our understanding that both are planned. > Regarding "authors' responsibility to show that their proposal is > likely to > stimulate research that might not otherwise be undertaken". It would appear to > me that the main audience that needs to hear about this research is the CDF > collaboration as they are the only ones able to carry out this proposed physics > analysis in THIS MANNER. Perhaps there might be an argument that other > experiments eg the LHC experiments might learn from it - although much of the > discussion is very CDF specific, and I suspect the LHC bunch structure and > intrinsic calorimeter timing resolution make it hard to apply. I also note that > eg. the Chen and Gunion paper (1997) already addresses much of the material here > in a much more general, albeit more phenomenological, way. Anyway - the authors > haven't demonstrated that this would stimulate research that might not otherwise > be undertaken outside of the CDF collaboration." A few more notes are appropriate here. We see no reason to think that our results are not applicable to the LHC and have made this more explicit in the text. The paper of Chen and Gunion (1997), while an excellent paper that suggests many useful things, it gives no quantitative phenomenology prospects for the Tevatron using long-lived particles and timing. Finally, while the criteria of "demonstrating that we would simulate research which might not otherwise be undertaken" is an inappropriate requirement on our paper in the first place, we see no reason why proving that the prospects are exciting, and perhaps stimulating FUNDING for the people to do the work, is not a worthy task. ****************** Now to the "Comments on the paper itself": > > o Extrapolating from published papers by a factor of 20 in luminosity > with a different detector without really any recent data studies > to back it up looks precarious. > > > > We think a factor of 20 for largely similar detectors is certainly justifiable and fairly common. The papers listed above contain estimates of signal and background data for luminosities of orders of magnitude beyond the what we have shown. By way of comparison, the extrapolations to LHC and SSC are FAR more precarious then our extrapolations in many different ways. > > > a) There seems to be some disconnect between eg. TABLE III and > reference 10. Ref. 10 has an acceptance cut of ET > 55 GeV not > 25 GeV as stated in text. > If the cut was 25 GeV, I'd expect much more Z gamma SM > background. > > Agreed. This has been fixed and made more explicit in the text. Thank you for pointing it out. > > > > Ref 10. says 12 events in 87 pb-1, this says 12.6 in 100pb-1. > > > Table I in Ref. [10] shows that the number of observed events are 11 in 87 pb-1 which is scaled to 12.6 in 100 pb-1. One could argue that we should have used the estimated 12 events. However a measured number is better and the difference is small when compared to our conservative background uncertainty estimate of 30%. > > > > > b) with the different bunch structures from runI to runII and > different expected integrated live-times of the EM_Calorimeter, > I'd expect that one should not extrapolate cosmics based on integrated > luminosity. The conclusion might be that cosmics are much less of an > issue if 2 fb-1 is really going to be delivered fairly quickly. > The paper has no discussions on detector gating issues - > indicating lack of attention to experimental detail relevant to > this type of search. > > > > The referee is quite right that the bunch structures are different in Run I and Run II. This has NOT been ignored rather it was just not explicitly discussed in an effort to cut down on the detail in the paper (which, we note, was described by the referee as verbose). Again we would like to emphasize that this is a phenomenological paper. We have no intention of discussing detector specific issues (see our comments in the beginning; also see the large uncertainties in Table I). Furthermore, the referee correctly points out that with the smaller bunch structure that the cosmic ray backgrounds will go down, so that all the estimates we have made are conservative (adding to the robustness of our result). Finally, the issue of the rate of cosmics is dealt with head-on in a separate section where we detail how our results might change if the cosmics fractions are mis-estimated. > > o several assumptions in the introduction indicate that the depth > at which this study convincingly demonstrates that the measurement > is definitely feasible is a bit lacking. I would have expected > that the authors would have done more to evaluate the effect on > the acceptance and photon-ID from the photons not pointing. > This is particularly relevant to the "low boost" part where the > timing separation is significant. > We agree that the effects on the photon-ID from photons not from the primary vertex might be significant. However these effects have been dealt with at other detectors, notably ALEPH. This was mentioned openly in the introduction, however we have made it more explicit that before any such analysis is to be pursued, both hard and important ID/acceptance studies are required. This we hope will initiate studies that might not otherwise be done, as it has not been done in 30 combined years at CDF/DZero. Again, not having ALL the experimental details worked has never been an impediment to publishing phenological work. > > > o These two comments suggest to me that the authors have not really > yet done much of the groundwork needed to carry out such a measurement > should they have the data on tape. > See previous responses on this type of comment. > > > o the paper suggests that only m_gravitino < 1 keV is cosmologically > interesting AND theoretically favored. > > This does not seem to be justified at all in reference 14, > which I note was not refereed. > > We have softened the 1 keV statement since it really isn't a hard bound, but rather 1 keV is just a good guide. A few keV is more appropriate and we have made the text reflect this. We note that the citation specifically indicated "and references therein" which contains links to refereed papers. In any case, we have made this more explicit, and referenced directly refereed papers. We say more on the issue below. > > > o My general impression of these GMSB studies is that there is no > really solid theoretical guidance on what is "theoretically favored". > Chen and Gunion (in ref. 5) note that m_gravitino should be < FEW keV > in "most cosmological scenarios [6,7]". They chose < 2.5 keV. > CG References [6,7] suggest to me that the < 1 keV number > sometimes quoted in the literature comes from an early paper which did > not consider possible additional effects in the cosmology. > In particular, CG ref 7, suggests to me that 100 keV is a priori more > interesting > based on known sparticle mass limits and suggests ways in which the > cosmology could have dilution mechanisms (of gravitino mass > density). Reading papers on this topic, in particular the papers referenced in CG, shows that a bound of "a few keV" is quite important from a theory point of view following in principle the argumentation in the early paper by Primack and Pagels (Phys. Rev. Lett. 48 223). In general the gravitino mass density causes the universe to overclose if it is heavier than 1 keV. This however does not affect the validity of this GMSB model. If one considers the effects of inflation ("dilution mechanisms") then this bound is softened to "a few keV" in most cosmological models. The vagueness in this limit is mainly due to a scale uncertainty in the inflationary models. What makes the region m_Grav > a few keV "theoretically unfavorable" is that one does not want to have these inflationary effects play a role in cosmological models, which would introduce an unnecessary difficulty. Moving to even higher gravitino masses, the dilution mechanisms become even more important. Note that the gravitino mass bound would not lead to an exclusion of the GMSB model. However, we agree that a more precise statement on the impact of the prospects is warrented. To this effect, we have put in more careful statements. Also, it might indeed be interesting to see how our results change if one were to choose different GMSB parameters which we have not done. > > > I think it is fair to say that this paper indicates that the sensitivity > of the CDF experiment can be extended in lifetime by about a > factor of 1.5 with this EMtiming technique (over pointing alone in CDF). > Having 2 techniques is very good for any potential discovery. > However I think it is misleading to give the impression that with this > analysis all the theoretically favored and cosmologically > allowed parameter space would be covered. > We basically agree with the assessment that we have shown a significant improvement in the sensitivity and, as mentioned above, we have been more precise about the prospective exclusion regions and their relation to cosomologically favored regions. > > It is my understanding that lifetimes of order 10^4 - 10^8 s are > even under consideration in related models. > > We are assuming the referee means "10^(-4) - 10^(-8) s"? In any case, we are not aware of any other serious models that would predict neutral, long-lived neutralinos (or other particles) that decay to photons. We would be obliged if the referee would provide us with one. > > > > > o LHC. You may want to consider discussing whether or not such > sensitivity is also possible at the LHC. > > > We agree that this might be interesting to do. However, there are experimental issues which can have a big effect. The biggest, we think, is the calorimeter gating and smaller bunch spacing which might make a photon from a long lived neutralino show up in the next bunch crossing. To make robust predictions at this point is precarious and would be, in our opinion, a separate study. On the flip side, positive effects might come from a smaller beam spot. Surely the mentioned issues are interesting to study, but, again, looking at the cited papers above, we don't see why it would hinder the publication of this paper not to additionally extend our analysis on those issues. > > > o contradictory figures. some figures have 110 GeV but captions have 70 GeV. > If the intent is really to demonstrate complementarity to LEP it would be > more representative if all such figures were for 110 GeV. > > This mistake should not have happened. The data in the plots was correct, just the labeling was broken. For consistency all figures related to cross section limits were produced for 110 GeV. We now changed all Figs., including 2,4,5 and 9, to a mass of 110 GeV. Apologies for the confusion. > > > o many "<" and ">" are mistyped or funny font. > > > We do not understand where in the paper this comment refers to. Throughout the text we used the same Latex-notations as in previously published PRD papers. If the referee sends us an example (ps-file), we are happy to fix this problem. > > > > o In a paper which contrasts both existing limits based on data (ALEPH) > with prospective limits estimated from simulation IF 2 fb-1 is collected, > care should be taken in comparing the two types of information. > A luminosity of 2fb-1 is considered easily reachable in the coming Run II at the Tevatron. The criticism is justified though. In our new draft we are more explicit about the prospective in contrast to existing limits. > > > A legitimate question might be: Is there any region where a 5-sigma > signal could be robustly observed with 1 fb-1 which is > not already excluded ? > > > > See the comment below! > > > It is not really feasible for the reader to evaluate this since > no comparisons of signal and background event counts are given. > > This is a legitimate criticism. To address this we have included a table (Table V) that shows information on signal and background for some points in the mass - lifetime plane. From these numbers one can easily calculate e.g. 5 sigma excesses at these points in parameter space. Further we added a Figure of how the signal would show up for the optimized MET cut as a function of delta_s. We hope that this helps understanding the process and thank the referee for helping generate these ideas which clearly improve the clarity of the paper. > > > o The LEPII exclusion is actually just from the ALEPH experiment - and it > should say so. Where appropriate it would be reasonable to > also refer to other results from LEP experiments. > > > o In particular, I suspect there are more stringent limits from LEP > available at least in the form of preliminary results. > > There are no other published results from other collaborations which are relevant here that we know of. ALEPH has the most stringent limits. The reference shows that these are ALEPH-only results. That these limits are from ALEPH has been emphasized more properly in the text. > > > > o I suspect the ALEPH results are more general. Does the GMSB model used > really allow comparison of the Tevatron prospects and LEP data ? > Yes, the ALEPH exclusion regions were calculated from a scan over a large part of GMSB parameter space. We corresponded with the person who was in charge of the analysis at ALEPH to make sure we got the comparisons right. He produced a plot that showed the ALEPH limits for the GMSB parameters we used, which we show in Fig. 17. There were no visible changes in exclusion region. He is happy with the result and we have more explicitly cited his contribution. > > It would seem to me that the Tevatron cross-sections depend sensitively > on the gluino and squark masses, while for the LEP analyses > the actual parameters that matter are indeed the > neutralino mass and lifetime. > Again, the plot needs to make it clear that these are not really > apple with apple comparisons. > As mentioned above, we compare the LEP exclusion region for our parameter combination with our results. Thus, the comparison is apple with apple. We agree that any exclusion region depends on these types of parameters. For that reason we have large systematic errors which, in our experience and judging from the literature, easily cover these types of variations. > > > o The reference by D0 authors in [12] indicates impact > parameter resolution of about 1.5 cm for D0. > The photon pointing Appendix which indicates that timing is a better tool > for CDF than pointing should point out that the plots are just for CDF > and that D0 should have much better sensitivity using pointing. > In the 2nd line of the section we write: "... we compare the EMTiming system to a potential pointing ability at CDF." It is certainly true that D0 should have good sensitivity with an impact parameter resolution of 1.5 cm. We hope the text is now sufficiently explicit. > > o particularly sections II and III are fairly verbose with a lot of material > which was not presented in a very insightful way. For example, > why present "perfect measurement" cases for efficiency estimates. > Surely only those including resolution are relevant ? > The substance of this criticism is legitimate and very helpful. As previously mentioned, we have moved section II to an Appendix. We have made the main text such that all results take into account measurement uncertainties. We hope to have made the paper more transparent this way. > > > o Appendix A formula should have a factor of 7/9 in the argument of the > exponent. > > That's right. Apologies for this mistake in the equation. We added the reference for the PDG booklet where this formula is described. While it has no substantive effect on the results we have fixed the plot. > > > o Fig 18. "doubles" -> "halves" ? > > The statement in the text must have not been explicit enough. The cross section limit will be doubled, not halved, leading to a smaller exclusion region. We corrected this statement to make it more obvious. > > > O p23. "result" -> "prospective result" (again distinction between a > result and a prospect) > > > > Thanks for pointing this out. We fixed this (see also comments above). Again, we thank the referee for their useful comments and believe that our paper is the better for it. We hope that given the arguements above a reconsideration of our case is possible, and that it will lead to a favorable outcome. Regards, Peter Wagner and Dave Toback