Dear Brahmin, I get to work on these fixes ASAP. Michael Begin forwarded message: > From: <prc_at_aps.org> > Date: February 11, 2011 1:30:28 PM CST > To: <mjmurray_at_ku.edu> > Subject: Your_manuscript CS10219 Arsene > Reply-To: <prc_at_aps.org> > > Re: CS10219 > Rapidity dependence of deuteron production in central Au+Au collisions > at sqrt s NN=200 GeV > by I. Arsene, I. G. Bearden, D. Beavis, et al. > > Dear Dr. Murray, > > The above manuscript has been reviewed by one of our referees. Comments > from the report appear below. > > These comments suggest that specific revisions of your manuscript are > in order. When you resubmit your manuscript, please include a summary > of the changes made and a succinct response to all recommendations or > criticisms contained in the report. > > Yours sincerely, > > Lin Zhang > Senior Editorial Assistant > Physical Review C > Email: prc_at_ridge.aps.org > Fax: 631-591-4141 > http://prc.aps.org/ > > Physics - spotlighting exceptional research: http://physics.aps.org/ > > P.S. We regret the delay in obtaining this report. > > ---------------------------------------------------------------------- > Second Report of the Referee -- CS10219/Arsene > ---------------------------------------------------------------------- > > Executive Summary: > ------------------ > > The manuscript has been noticeably polished in the second/resubmitted > version, and in general the authors' response to the original referee > comments has been attentive. A number of small problems/flaws remain, > which are detailed below; these should be fairly straightforward to > address. I would recommend publishing the paper with only minor > corrections, and no further review should be required. > > > Detailed Remarks, in order through the MS: > ------------------------------------------ > > Page 1 > > 1) There appears to be a typesetting artifact in the footnote > superscript following author Z. Yin's name in the author list, and in > the corresponding footnote at the bottom of the page. > > 2) "enables this 2->1 process to proceed while it conserves > energy...": "it conserves" would be better as "conserving". > > 3) Regarding the sentence "In the hot and dense system produced in > high-energy ion collisions, the coalescence of nucleons into deuterons > is not possible before the system reaches a stage where hadrons are > present." This is certainly true, but it seems rather trivial, almost > tautological, to say that nucleons can't coalesce before hadrons even > exist. As it stands this sentence conveys no information or logic, and > so is odd and jarring to read. I guess that the authors' intent was > not perfectly captured here. > > 4) "...high enough to allow for interactions that put all participants > back on mass shell". I find this sentence very confusing; in general, > interactions _don't_ put particles back on mass shell, they do just > the opposite by providing access (ie non-zero transition matrix > elements) to states in which particles are off shell. What's being > implied here is that, all of a particle's early history of collisions > can put it off mass shell, but then its very last interaction somehow > -- magically? -- puts the particle back on shell; as stated it really > makes no sense and I think this sentence needs to be logically > re-worked. > > I don't mean to dictate the prose at all, but will remind the authors > of the coalescence conception I referred to in the first set of > comments: after the last significant interaction by the particles the > amplitude for off-shell states decays away naturally (in accordance > with Heisenberg, if you prefer that language) and only the states > corresponding to stable, on-shell particles (including bound states > such as the deuteron) will persist. There is no need to invoke > interactions as the mechanism for returning particle to their mass > shells in the long-term final state. > > Page 2 > > 5) In Equation 1, it should be made clear that B_2 is in principle a > function of the full, 3-D proton (or deuteron) momentum, and not just > transverse momentum. The observation that B_2 seems to be independent > of rapidity is an interesting experimental fact, but one which comes > much later in the paper and involves only this specific data set. At > this point, where the general relationships and quantities are being > defined it is misleading to imply that B_2 is a function of p_T as a > matter of definition or principle. (Also, the text does not identify > explicitly whether this p_T is the transverse momentum of the proton > or the deuteron, one indicator of the weakness of this construction.) > The same critique applies equally to Equations 2 and 9 as well. > > 6) In the text following Eq. 1 the phrase "it is assumed" appears to > apply to the equivalence between the deuteron momentum and twice the > proton momentum. This is not really correct; the equivalence is a > matter of definition in the terms of Eq. 1, not an assumption. > Similarly, the statement that the deuteron momentum is the sum of the > nucleon momenta is generic to all coalescence pictures and is not > particular to Eq. 1 here. > > 7) The relationship to the unmeasured neutron spectrum is also > presented in a confusing way here. First, Eq. 1 does not generally > assume that the neutron spectrum is identical to the proton spectrum > in a coalescence picture, _unless_ B_2 is constant across all momenta > -- and even in that case it only implies that the neutron spectrum and > proton spectrum are proportional, not identical. But since Eq.1 > explicitly considers the possibility (as borne out in the data) that > B_2 is not constant across all momenta, no assumption about the > neutron spectrum is actually embodied in, or required for, Eq. 1 to be > operative. It is only when a specific coalescence mechanism is > invoked, such as that leading to Eq. 2 involving the deuteron > wavefunction, that the assumption about the neutron spectrum needs to > be made. > > 8) As a matter of curiosity, when the n/p ratio changes in the > low-energy data from 1.52 in the beams to 1.19 in the secondary > nucleons, where does the rest of the isospin go? Is it known to be in > the pion sector? or the kaon? It's only tangentially related to the > argument here, but it might give the reader comfort to know that the > missing isospin has in fact been found elsewhere. > > 9) In the text "effective volume ... at the time of coalescence" the > latter phrase is not really defined. Does this mean at the time of > freezeout, assumed to exist in some kind of sudden approximation? In > order to define the homogeneity volume sensibly -- which is certainly > important -- this "time of coalescence" needs to be better defined as > an ingredient. Remember, there is a reasonable view, as above, that > coalescence doesn't happen at any specific time but evolves on a > timescale on the order of hbar/2MeV, which is much longer than the > time for hydro evolution in a RHIC collision, so more careful > definitions are definitely called for here. > > 10) In the phrase "space averaged phase-space", "space averaged" could > be considered a compound adjective and so should be hyphenated, ie > "space-averaged". Note that the same may apply to "so called" later in > the same column. > > 11) The text "overlaps of the nucleon wavefunctions and the deuteron > wavefunction as the coalescence function.", is quite confusing because > the phrase "coalescence function" has not been defined so far, and in > fact is never explicitly defined in the paper. This confusion could be > cleared up with the use of another equation illustrating how the > deuteron wavefunction enters into the coalescence probability, which > would then make the origin of Eq. 2 much clearer. > > 12) In the last sentence of the first column on Page 2, do "Gaussian > distribution" and "Gaussian spatial profile" mean the same thing? If > so, it's confusing to read the two different terms; if not, then it's > not at all clear what is meant by either. > > 13) It is not clear what the phrase "this comparison also works well > for our data" means; if the source size estimates hadn't matched up, > does that mean the "comparison didn't work well?" It doesn't really > make sense to say that a comparison "works" or not; what works (or > not) are specific models that make specific predictions, such as that > these two estimates should agree. This could use re-phrasing. > > 14) "At lower energies R_G has been found..." Does this refer to lower > beam energies, or lower secondary energies? > > 15) In the last paragraph of Section A, describing the variation of > B_2 versus energy in previous measurements, it would be very useful > for the reader to get a general idea of how large these variations are > quantitatively, ie how much is B_2 seen to change with energy? is it > by 10%? or 50%? or factors of x10? > > 16) Regarding the beginning of Section B. on the average phase space > density, I would generally say that the exposition is quite out of > order with terms being used in confusing and unhelpful ways well > before they are even defined. The leading example is right in the > first paragraph of this section, with the sentence "At SPS energies, a > system of massless bosons in thermal equilibrium would have a > space-averaged phase-space density of ~0.37." Since this averaged > density has not even been defined at this point, this sentence is > certainly confusing and at best a distraction. But even with the > definition provided later, it is not at all clear what if anything we > are supposed to learn from this sentence. Is a value of 0.37 high? or > low? What would it indicate if this number were 1.0? doe it have some > kind of natural maximum or minimum? Does this value for a massless > boson system come out of some kind of theoretical calculation? If so, > that should certainly be noted. Related: what does "at SPS energies" > mean? relative to the supposed system of massless bosons? is this a > roundabout way of specifying a (presumed) energy density? if so, then > what is that energy density? If not, then what feature of the SPS beam > energy is relevant here? But, wouldn't a system of massless bosons, > such as photons, have the same phase space occupancy at all > temperatures and densities? and so why is the SPS beam energy > particularly relevant at all? > > As should be clear, the presentation of this single sentence raises > far more questions than it answers! I can't go into detail on every > sentence here; but I can make the general statement that this section > could be greatly improved by making the definitions of the basic > quantities clearer, explaining their meaning and interpretation more > precisely and at greater length, and presenting them in a logical > order. > > Page 3 > > 17) On the same theme as remark 16, the phrase "volume of homogeneity" > has not been at all rigorously defined up to this point. > > 18) In the phrase "strong longitudinal flow could significantly reduce > the pion phase-space density", does this refer to the space-averaged > density? or to the density at specific points in phase space? > > 19) In Eq. 7, and the text just preceding it in the in-line equation > "P=2p", neither "P" nor "p" have yet been defined. If these are > (presumably) the deuteron and nucleon momenta, then shouldn't their > notations be consistent with Eq. 1 and Eq. 8? > > 20) At the end of Section I, the phrase "This was checked" refers to > the comparison between size parameters from coalescence and HBT > analyses in SPS collisions. Was the same check done in RHIC data, at > least at mid-rapidities, before the present work? Certainly this is > not the fist publication on deuterons at RHIC, at least at > mid-rapidity. > > Page 4 > > 21) Continuing from the previous page, the section II.A on the > detector system is hard to interpret without a picture or diagram of > some kind. Also, can some statement be made as to the acceptances of > the spectrometers? since these are a distinguishing factor for the > experiment. > > 22) The phrase "uncertainty in the centrality determination" being > +-4% is not well-defined. What selection in centrality is nominally > being attempted to measure? Multiplicity? Et? Impact parameter? Does > the 4% uncertainty mean the size of the bin, or the sharpness of the > cuttoff? > > 23) "proton deuteron PID separation" might be better as > "proton/deuteron PID separation" > > 24) Is there a reference which describes the RICH PID system in more > detail? if so, it would be useful to see it referred to in Section > II.D. Out of curiosity: are muons ever identified separately from > pions at any momenta? would you expect to see a significant number? > from any kind of hadron decay. > > Page 5 > > 25) In the text immediately after Eq. 10, the word "primary" is > somewhat confusing, since "primary" is often used to denote incoming > beam particles, as against "secondary" particles which emerge from the > collision. Here I guess "primary" means "not from weak decay", but > this could probably be worded better. > > 26) When we read that "The inverse slopes of the deuterons are on > average a factor of 1.6+-0.1 higher than those of the protons", what > kind of average is this? Is it over all the rapidity ranges? is it a > ratio of the average slope parameters over all rapidities? or an > average of the ratio at all rapidities? > > Page 6 > > 27) In Fig 4, why are the B_2 results shown for such a small range in > pT? For example, if there are six points measured for deuterons in the > 1.5<y<2.5 bin in Fig 3, then why is B_2 derived for only two of those > points in Fig 4? The statistical errors on the 2.8<y<3.2 bin are no > better in Fig 3, and yet three are plotted in Fig 4. Also, the error > bar on the higher pT point in the 1.5<y<2.5 panel of Fig 4 seems > anomalously large compared to that shown for the deuteron point in Fig > 3. > > Also, the caption for Fig 4 should describe what the error bars > indicate. > > Page 7 > > 28) In Fig 5 there should be a key to the symbols, and also an > explanation of the error bars. > > 29) When the results of Fig 5 are first mentioned in the text, if > these are derived from Eq. 8 then it would be good to refer back to > Eq. 8 at that point. > > Also, the second paragraph here describes changes in the averaged > phase-space density measurement versus pT. But, what physics do we > learn from this observation? This is a continuation of remark #16 > above, that the physical meaning of this observable hasn't really been > satisfactorily explained in the paper for the reader to understand the > significance of the pT dependence. > > 30) In describing what is shown in Table II, the phrase "in stark > contrast" seems like something of an over-statement. The SPS energy > results do show more of a monotonic trend, but within the errors on > the highest rapidity point it's not clear how significant that is. As > for the range of values, the SPS data vary by a factor of 13.7/7.9 ~ > 1.7 while the RHIC data vary by 10.6/6.6 ~ 1.6; this is hardly a stark > contrast between the two. Generally, if the authors want to claim that > one data set shows a trend with rapidity and that the other does not, > then it would be better to show these data in a figure and also make > an appropriate statistical test for the hypothesis. > > Page 8 > > 31) In the caption for Table II, the words "for at" are probably meant > to be just "at". > _______________________________________________ Brahms-dev-l mailing list Brahms-dev-l_at_lists.bnl.gov https://lists.bnl.gov/mailman/listinfo/brahms-dev-lReceived on Fri Feb 11 2011 - 14:36:46 EST
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