[Brahms-l] Fwd: Your_manuscript LQ9030 Arsene

Finally we have the reply from the editor.
The paper committee will work on preparing responses to each of the 
comments.

Ramiro

Begin forwarded message:

> From: Physical Review Letters <prl@ridge.aps.org>
> Date: June 28, 2004 2:50:18 PM EDT
> To: debbe@bnl.gov
> Subject: Your_manuscript LQ9030 Arsene
>
> Re: LQ9030
>     Evolution of the nuclear modification factors with rapidity and
>     centrality in d+Au collisions at $sqrt s sub {NN}$=200 GeV
>     by I. Arsene, I.G. Bearden, D. Beavis, C. Besliu, B. Budick, et al.
>
> Dr. R.R. Debbe
> Bldg 510D
> Brookhaven National Laboratory
> P. O. Box 5000
> Upton, NY 11973-5000
>
> Dear Dr. Debbe,
>
> The above manuscript has been reviewed by our referees.
>
> The resulting reports include a critique which we feel is serious
> enough that it must be answered before we can reach a decision on the
> disposition of the paper.  We enclose pertinent comments.
>
> You may choose to resubmit the manuscript with revisions you find
> appropriate.  Please accompany any resubmittal by a summary of the
> changes made, and a brief response to all recommendations and
> criticisms.
>
>
> Yours sincerely,
>
> Christopher Wesselborg
> Senior Assistant Editor
> Physical Review Letters
> Email: prl@aps.org
> Fax: 631-591-4141
> http://prl.aps.org/
>
> P.S.  We regret the delay in obtaining these reports.
>
>
> ----------------------------------------------------------------------
> Report of Referee A -- LQ9030/Arsene
> ----------------------------------------------------------------------
>
> The measurements presented in this paper are of utmost importance to 
> the
> field of relativistic heavy ions and to the physics community as a
> whole. There is no doubt that evidence for gluon saturation effects at
> low-x would be of interest not only to Nuclear Physicists. Therefore
> these data should be published by PRL as soon as possible, and I only
> have a few questions that need to be answered before I recommend
> publication of the paper in PRL:
>
> 1.) The compressed scale in Fig.2 in the paper makes the quantitative
> analysis of the data quite difficult. I much prefered the way the data
> were presented at the DNP fall meeting and the QM conference. But after
> careful checking I conclude that the data in the paper and the data
> shown at the conferences are consistent. So this is just my preference
> regarding plotsmanship and it should be taken as a suggestion.
>
> 2.)  I think the paper should clearly state the pseudo-rapidity bins
> that were used for the measurements rather than saying 'narrow 
> intervals
> around eta = 0,1,2.2,3.2'. How narrow ? And how does the narrowness
> affect the statistics ?
>
> 3.) What are the different colored contours in the upper row of Fig.1 ?
> They are neither explained in the text nor the figure caption.
>
> 4.) Fig.6 top: 'based on simulations the ratios calculated with 
> negative
> particles are larger in forward rapidities than the ones calculated 
> with
> the charge average.' Why ? By how much ? Is that in the systematic 
> error
> ? Could it be corrected on the basis of the simulations ? Has that been
> done for the data presented here ?
>
> 5.) Fig.6 middle: 'strong correlation between ratio of charge particle
> eta densities and R(dA) values.' What does that mean ? Maybe one
> sentence of explanation should be added here and not just two
> references. What are the physics implications ? And how strong is that
> correlation ? It seems correlation in this context is defined as the
> fact that the R(dA) values in the lowest pt bin shown here reach the
> dashed line. Well, the lowest pt bin shown varies from eta-bin to
> eta-bin. Is there a claim that the R(dA) values would be constant below
> the lowest measured bin and therefore follow the density ratio line ? 
> Is
> this an indirect argument for participant scaling at low pt ? Please 
> add
> a sentence about the physics relevance of this agreement between R(dA)
> and particle density ratio.
>
> 6.) Fig.7 end of first paragraph: 'the functional form of the c-to-p
> ratio is close to that of the saturation scale.' Which functional form
> of the saturation scale ? The one shown on page 3: Q**2 prop. e(Lambda
> y) ?  So Lambda is 0.2-0.3 based on HERA data and alpha on page 7 is
> -0.28 based on BRAHMS data. Is that the connection ? Please elaborate 
> by
> adding one sentence of explanation. Also, the saturation scale in HERA
> is measured in rapidity not in pseudorapidity. Wouldn't that cause a
> difference to the functional form at very forward rapidities ?
>
> 7.) Fig.8 in the summary: a.) 'results are consistent with a
> modification of the Gold wave function'. I am not sure whether the 
> 'Gold
> wave function' here is not too generic a term. I am not really sure 
> what
> the authors mean by modification to the Gold wave function. b.) next
> sentence: 'such modifications produced a suppression at all values of 
> pt
> similar to the multiplicity density ratio.' So this goes even further
> than the statement in the text to Fig.2 where it was stated that the
> R(dA) values reach the particle density ratios at low pt. Here now the
> modifications is the same for all pt's. I guess this relates to the
> solid symbols in the last panel of Fig.3. Again, the relation between
> particle density and suppression factor is not explained. Is the fact
> that for this bin the R(dA) are near constant an indication of an
> initial state effect ? How does this relate to the statement in the 
> text
> about Fig.2 ? c.) I think the final sentence of the paper should be
> taken out because it states a preference in the interpretation of the
> data that can not yet be unambiguously corroborated. The paper nicely
> states the alternate HIJING based approach that utilizes increased 
> gluon
> shadowing. Maybe the difference between color glass condensate and
> strong gluon shadowing is just semantics, but I would not claim 
> evidence
> for gluon saturation on the basis of this measurement alone. The data
> are very exciting in their own right and do not require a statement by
> the experimentalists on the ongoing model controversy.
>
> 8.) some typos: a.) p.6 near the end: ...collisions (12%). Which is a
> conservative....
>      should be: ...collisions (12%), which is a conservative....
> b.) references not in proper order: there is a gap from [13] to [19]
>      which gets filled later.
> c.) references: some of them have bold numbers, some of them don't.
>      Please make them all consistent.
>
> Otherwise this is a very nice paper. I am looking forward to the
> response to my inquiries, and I will recommend publication as soon as
> these points are settled.
>
>
>
> ----------------------------------------------------------------------
> Report of Referee B -- LQ9030/Arsene
> ----------------------------------------------------------------------
>
> This is a very important result, and the paper should ultimately be
> published in Physical Review Letters. However, there are some things
> which need to be clarified and/or corrected before the paper should be
> published.
>
> The most important issue to be addressed is that the data shown in 
> figures
> 1, 2 and 3 do not appear to be consistent. The main message of the 
> paper, a
> decrease in particle yield in dAu compared to pp with increasing 
> rapidity,
> is clearly visible in figure 3. However, in figure 2 the suppression 
> effect
> appears to be significant only at the approximately 2 sigma level. The
> nuclear modification factor from the yield ratio in central to 
> peripheral
> collisions has been observed to exceed the nuclear modification factor
> calculated by comparing to p+p collisions. Indeed this is the case for 
> the
> data in this paper at pseudorapidity 0 and 1 and at low pT for more 
> forward
> rapidities. However, for high pT at forward angles the trend appears
> reversed. This prompted me to attempt to recalculate RdAu in figure 2 
> from
> the spectra in Figure 1 using equation 1 and the given value of 
> <Ncoll> =
> 7.2. I was able to reproduce plotted RdAu values for the three lower 
> rapdity
> bins. However, the rightmost panel of figure 2 is simply not 
> consistent at
> higher pT with the spectra presented in figure 1 for negatively charged
> particles at pseudorapidity = 3.2! At the highest pT bin, the d+Au 
> spectrum
> actually falls below that in p+p, yet the RdAu reported in Fig.2 for 
> that pT
> bin is not the smallest value for pseudorapidity = 3.2. It is not 
> possible
> for this reviewer to determine whether Figure 2 is incorrect or Figure 
> 1 is
> incorrect, but one of them must be.
>
> It is absolutely imperative for the collaboration to sort this out, as 
> this
> is the only rapidity range where the traditional nuclear modification 
> factor
> shows a suppression in d+Au collisions. Looking at the spectrometer
> acceptance plot in the upper part of figure 1, one notes that the 
> acceptance
> at this setting is quite tiny. Furthermore, based upon the figure, the 
> small
> acceptance results in few particles measured, which must cause 
> considerable
> uncertainty on the acceptance correction. Undoubtedly many Monte Carlo
> events were generated to study this, however, the reader is given no 
> measure
> of how well this correction has been determined. Since the acceptance
> correction clearly must be very large, the authors need to recheck 
> that this
> is done properly, state the magnitude of the correction and the 
> uncertainty
> on it. It is very difficult to accept that the systematic uncertainty 
> on the
> forward spectra at high pT in Fig. 1 is the same 15% as where the
> spectrometer acceptance is large and easily determined. In the ratio 
> of d+Au
> to p+p collisions, much of this uncertainty may be expected to cancel.
> However, it is clear that this ratio will still reflect residual
> uncertainties in the reproducibility of positioning the forward 
> spectrometer
> at 4 degrees. The authors should state the magnitude of this 
> uncertainty
> explicitly, as the main conclusion of the paper rests so heavily on 
> this
> spectrometer angle.
>
> As it is so important to the conclusion of the paper, which may be the 
> first
> observation of gluon saturation in nuclear collisions, further 
> clarification
> is needed for figure 3, as well. Because the suppression is more 
> apparent in
> this variable, it is important to also publish the centrality selected
> spectra upon which this ratio is based. The statistical errors on the
> minimum bias spectra are not visible in figure 1, and the shape as 
> well as
> value of the nuclear modification factor is very different in figures 
> 3 and
> 2. I would therefore like to see the paper include the centrality 
> selected
> spectra, perhaps as a second set of panels to Fig. 3.
>
> In the physics discussion in the last two paragraphs of the paper, 
> there are
> several issues, as well. The penultimate paragraph discusses two models
> incorporating related, but quantitatively different, physics 
> assumptions.
> However, it does not give a clear message to the reader. Do the data 
> prove
> that one model is closer to the truth than the other? The concluding
> paragraph appears to indicate that this is the case, but includes a 
> sentence
> whose meaning I was unable to figure out. Can the authors please 
> replace
> this sentence "Such modification produces a suppression at all values 
> of pT
> similar to the one observed when comparing multiplicity densities." 
> with
> something simpler and clearer? Presumably "the one observed" refers to 
> the
> amount of suppression, not the pT values... ? Also, for the general 
> reader
> of PRL, it would be useful if the pT range in which suppression is 
> observed
> were related back to the value of Q_s expected for the relevant 
> rapidity
> range to support conclusions about the gold wavefunction at small x.
>




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