Click here for second round.

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Report of Referee A:

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This is really a well-written paper. It was a pleasure to read, and I

have only relatively minor comments.

We thank the reviewer for careful reading of our paper and for providing

useful feedback. We are pleased to know that the reviewer finds the

paper to be well written. We have incorporated all the comments into a

new version of the draft.

Page 3: Although there aren't published pp upsilon cross sections there

is a published R_AA and an ee mass spectrum shown in E. Atomssa's QM09

proceedings. This should be referenced.

We are aware of the PHENIX results from

E. Atomssa, Nucl.Phys.A830:331C-334C,2009

and three other relevant QM proceedings:

P. Djawotho, J.Phys.G34:S947-950,2007

D. Das, J.Phys.G35:104153,2008

H. Liu, Nucl.Phys.A830:235C-238C,2009

However, it is STAR's policy to not reference our own preliminary data on the manuscript we submit for publication on a given topic, and by extension not to reference other preliminary experimental data on the same topic either.

Page 4, end of section A: Quote trigger efficiency.

The end of Section A now reads:

"We find that 25% of the Upsilons produced at

midrapidity have both daughters in the BEMC acceptance and at least one

of them can fire the L0 trigger. The details of the HTTP

trigger efficiency and acceptance are discussed in Sec. IV"

Figure 1: You should either quote L0 threshold in terms of pt, or plot

vs. Et. Caption should say L0 HT Trigger II threshold.

We changed the figure to plot vs. E_T, which is the quantity that is

measured by the calorimeter. For the electrons in the analysis, the

difference between p_T and E_T is negligible, so the histograms in

Figure 1 are essentially unchanged. We changed the caption as suggested.

Figures 3-6 would benefit from inclusion of a scaled minimum bias spectrum

to demonstrate the rejection factor of the trigger.

We agree that it is useful to quote the rejection factor of the trigger.

We prefer to do so in the text. We added to the description of Figure

3 the following sentence: "The rejection factor achieved with Trigger

II, defined as the number of minimum bias events counted by the trigger scalers

divided by the number events where the upsilon trigger was issued, was

found to be 1.8 x 10^{5}."

Figure 9: There should be some explanation of the peak at E/p = 2.7

We investigated this peak, and we traced it to a double counting error.

The problem arose due to the fact that the figure was generated from

a pairwise Ntuple, i.e. one in which each row represented a pair of

electrons (both like-sign and unlike-sign pairs included), each with a

value of E and p, instead of a single electron Ntuple. We had plotted

the value of E/p for the electron candidate which matched all possible

high-towers in the event. The majority of events have only one candidate

pair, so there were relatively few cases where there was double

counting. We note that for pairwise quantities such as opening angle and

invariant mass, each entry in the Ntuple is still different. However,

the case that generated the peak at E/p = 2.7 in the figure was traced

to one event that had one candidate positron track, with its

corresponding high-tower, which was paired with several other electron

and positron candidates. Each of these entries has a different invariant

mass, but the same E/p for the first element of the pair. So its entry

in Figure 9, which happened to be at E/p=2.7, was repeated several times

in the histogram. The code to generate the data histogram in Figure 9

has now been corrected to guarantee that the E/p distribution is made

out of unique track-cluster positron candidates. The figure in the paper

has been updated. The new histogram shows about 5 counts in that

region. As a way to gauge the effect the double counting had on the

E/p=1 area of the figure, there were about 130 counts in the figure at

the E/p=1 peak position in the case with the double-counting error, and

there are about 120 counts in the peak after removing the

double-counting. The fix leads to an improved match between the data

histogram and the Monte Carlo simulations. We therefore leave the

efficiency calculation, which is based on the Monte Carlo Upsilon

events, unchanged. The pairwise invariant mass distribution from which

the main results of the paper are obtained is unaffected by this. We

thank the reviewer for calling our attention to this peak, which allowed

us to find and correct this error.

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Report of Referee B:

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The paper reports the first measurement of the upsilon (Y) cross-section

in pp collisions at 200 GeV. This is a key piece of information, both

in the context of the RHIC nucleus-nucleus research program and in its

own right. The paper is rather well organized, the figures are well

prepared and explained, and the introduction and conclusion are clearly

written. However, in my opinion the paper is not publishable in its

present form: some issues, which I enumerate below, should be addressed

by the authors before that.

The main problems I found with the paper have to do with the estimate

of the errors. There are two issues:

The first: the main result is obtained by integrating the counts above

the like-sign background between 8 and 11 GeV in figure 10, quoted to

give 75+-20 (bottom part of table III). This corresponds the sum Y +

continuum. Now to get the Y yield, one needs to subtract an estimated

contribution from the continuum. Independent of how this has been

estimated, the subtraction can only introduce an additional absolute

error. Starting from the systematic error on the counts above background,

the error on the estimated Y yield should therefore increase, whereas

in the table it goes down from 20 to 18.

Thanks for bringing this issue to our attention. It is true that when

subtracting two independently measured numbers, the statistical

uncertainty in the result of the subtraction can only be larger than the

absolute errors of the two numbers, i.e. if C = A - B, and error(A) and

error(B) are the corresponding errors, then the statistical error on C

would be sqrt(error(B)^{2}+error(A)^{2}) which would yield a larger absolute

error than either error(A) or error(B). However, the extraction of the

Upsilon yield in the analysis needs an estimate of the continuum

contribution, but the key difference is that it is not obtained by an

independent measurement. The two quantities, namely the Upsilon yield

and the continuum yield, are obtained ultimately from the same source:

the unlike sign dielectron distribution, after the subtraction of the

like-sign combinatorial background. This fact causes an

anti-correlation between the two yields, the larger the continuum yield,

the smaller the Upsilon yield. So one cannot treat the subtraction of

the continuum yield and the Upsilon yield as the case for independent

measurements. This is why in the paper we discuss that an advantage of

using the fit includes taking automatically into account the correlation

between the continuum and the Upsilon yield. So the error that is

quoted in Table III for all the "Upsilon counts", i.e. the Fitting

Results, the Bin-by-bin Counting, and the Single bin counting, is quoted

by applying the percent error on the Upsilon yield obtained from the

fitting method, which is the best way to take the anti-correlation

between the continuum yield and the Upsilon yield into account. We will

expand on this in section VI.C, to help clarify this point. We thank the referee for

alerting us.

The second issue is somewhat related: the error on the counts (18/54, or

33%) is propagated to the cross section (38/114) as statistical error,

and a systematic error obtained as quadratic sum of the systematic

uncertainties listed in Table IV is quoted separately. The uncertainty on

the subtraction of the continuum contribution (not present in Table IV),

has completely disappeared, in spite of being identified in the text as

"the major contribution to the systematic uncertainty" (page 14, 4 lines

from the bottom).

This is particularly puzzling, since the contribution of the continuum

is even evaluated in the paper itself (and with an error). This whole

part needs to be either fixed or, in case I have misunderstood what the

authors did, substantially clarified.

We agree that this can be clarified. The error on the counts (18/54, or

33%) includes two contributions:

1) The (purely statistical) error on the unlike-sign minus like sign

subtraction, which is 20/75 or 26%, as per Table III.

2) The additional error from the continuum contribution, which we

discuss in the previous comment, and is not just a statistical sum of

the 26% statistical error and the error on the continuum, rather it must

include the anti-correlation of the continuum yield and the Upsilon

yield. The fit procedure takes this into account, and we arrive at the

combined 33% error.

The question then arises how to quote the statistical and systematic

uncertainties. One difficulty we faced is that the subtraction of the

continuum contribution is not cleanly separated between statistical and

systematic uncertainties. On the one hand, the continuum yield of 22

counts can be varied within the 1-sigma contours to be as low as 14 and

as large as 60 counts (taking the range of the DY variation from Fig.

12). This uncertainty is dominated by the statistical errors of the

dielectron invariant mass distribution from Fig. 11. Therefore, the

dominant uncertainty in the continuum subtraction procedure is

statistical, not systematic. To put it another way, if we had much

larger statistics, the uncertainty in the fit would be much reduced

also. On the other hand, there is certainly a model-dependent component

in the subtraction of the continuum, which is traditionally a systematic

uncertainty. We chose to represent the combined 33% percent error as a

statistical uncertainty because a systematic variation in the results

would have if we were to choose, say, a different model for the continuum

contribution, is smaller compared to the variation allowed by the

statistical errors in the invariant mass distribution. In other words,

the reason we included the continuum subtraction uncertainty together in

the quote of the statistical error was that its size in the current

analysis ultimately comes from the statistical precision of our

invariant mass spectrum. We agree that this is not clear in the text,

given that we list this uncertainty among all the other systematic

uncertainties, and we have modified the text to clarify this. Perhaps a

more appropriate way to characterize the 33% error is that it includes

the "statistical and fitting error", to highlight the fact that in

addition to the purely statistical errors that can be calculated from

the N++, N-- and N+- counting statistics, this error includes the

continuum subtraction error, which is based on a fit that takes into

account the statistical error on the invariant mass spectrum, and the

important anti-correlation between the continuum yield and the Upsilon

yield. We have added an explanation of these items in the updated draft of

the paper, in Sec VI.C.

There are a few other issues which in my opinion should be dealt with

before the paper is fit for publication:

- in the abstract, it is stated that the Color Singlet Model (CSM)

calculations underestimate the Y cross-section. Given that the discrepancy

is only 2 sigma or so, such a statement is not warranted. "Seems to

disfavour", could perhaps be used, if the authors really insist in making

such a point (which, however, would be rather lame). The statement that

CSM calculations underestimate the cross-section is also made in the

conclusion. There, it is even commented, immediately after, that the

discrepancy is only a 2 sigma effect, resulting in two contradicting

statements back-to-back.

Our aim was mainly to be descriptive. To clarify our intent, the use of

"underestimate" is in the sense that if we move our datum point lower by the

1-sigma error of our measurement and this value is higher than the top

end of the CSM calculation. We quantify this by saying that the

size of the effect is about 2-sigma. We think that the concise statement

"understimate by 2sigma" objectively summarizes the observation, without

need to use more subjective statements, and we modified

the text in the abstract and conclusion accordingly.

- on page 6 it is stated that the Trigger II cuts were calculated offline

for Trigger I data. However, it is not clear if exactly the same trigger

condition was applied offline on the recorded values of the original

trigger input data or the selection was recalculated based on offline

information. This point should be clarified.

Agreed. We have added the sentence: "The exact same trigger condition was

applied offline on the recorded values of the original trigger input data."

- on page 7 it is said that PYTHIA + Y events were embedded in zero-bias

events with a realistic distribution of vertex position. Given that

zero-bias events are triggered on the bunch crossing, and do not

necessarily contain a collision (and even less a reconstructed vertex),

it is not clear what the authors mean.

We do not know if the statement that was unclear is how the realsitic

vertex distribution was obtained or if the issue pertained to where the analyzed collision comes from.

We will try to clarify both instances. The referee has correctly understood

that the zero-bias events do not necessarily contain a collision.

That is why the PYTHIA simulated event is needed. The zero-bias events

will contain additional effects such as out of time pile-up in the Time

Projection Chamber, etc. In other words, they will contain aspects of

the data-taking environment which are not captured by the PYTHIA events.

That is what is mentioned in the text:

"These zero-bias events do not always have a collision in the given

bunch crossing, but they include all the detec-

tor effects and pileup from out-of-time collisions. When

combined with simulated events, they provide the most

realistic environment to study the detector e±ciency and

acceptance."

The simulated events referred to in this text are the PYTHIA events, and

it is the simulated PYTHIA event, together with the Upsilon, that

provides the collision event to be studied for purposes of acceptance

and efficiency. In order to help clarify our meaning, we have also added

statements to point out that the dominant contribution to the TPC occupancy

is from out of time pileup.

Regarding the realistic distribution of vertices,

this is obtained from the upsilon triggered events (not from the zero-bias events, which

have no collision and typically do not have a found vertex, as the referee correctly

interpreted). We have added a statement to point this out and hopefully this will make

the meaning clear.

- on page 13 the authors state that they have parametrized the

contribution of the bbar contribution to the continuum based on a PYTHIA

simulation. PYTHIA performs a leading order + parton shower calculation,

while the di-electon invariant mass distribution, is sensitive to

next-to-leading order effects via the angular correlation of the the two

produced b quarks. Has the maginuted of this been evaluated by comparing

PYTHIA results with those of a NLO calculation?

We did not do so for this paper. This is one source of systematic

uncertainty in the continuum contribution, as discussed in the previous

remarks. For this paper, the statistics in the dielectron invariant

mass distribution are such that the variation in the shape of the b-bbar

continuum between LO and NLO would not contribute a significant

variation to the Upsilon yield. This can be seen in Fig. 12, where the

fit of the continuum allows for a removal of the b-bbar yield entirely,

as long as the Drell-Yan contribution is kept. We expect to make such

comparisons with the increased statistics available in the run 2009

data, and look forward to including NLO results in the next analysis.

- on page 13 the trigger response is emulated using a turn-on function

parametrised from the like-sign data. Has this been cross-checked with a

simulation? If yes, what was the result? If not, why?

We did not cross check the trigger response on the continuum with a

simulation, because a variation of the turn-on function parameters gave

a negligible variation on the extracted yields, so it was not deemed

necessary. We did use a simulation of the trigger response on simulated

Upsilons (see Fig. 6, dashed histogram).

Finally, I would like to draw the attention of the authors on a few less

important points:

- on page 6 the authors repeat twice, practically with the same words,

that the trigger rate is dominated by di-jet events with two back-to-back

pi0 (once at the top and once near the bottom of the right-side column).

We have changed the second occurrence to avoid repetitiveness.

- all the information of Table I is also contained in Table 4; why is

Table I needed?

We agree that all the information in Table I is contained in Table 4

(except for the last row, which shows the combined efficiency for the

1S+2S+3S), so it could be removed. We have included it for convenience

only: Table I helps in the discussion of the acceptance and

efficiencies, and gives the combined overall correction factors, whereas

the Table IV helps in the discussion of the systematic uncertainties of

each item.

- in table IV, the second column says "%", which is true for the

individual values of various contributions to the systematic uncertainty,

but not for the combined value at the bottom, which instead is given

in picobarn.

Agreed. We have added the pb units for the Combined error at the bottom of the

table.

- in the introduction (firts column, 6 lines from the bottom) the authors

write that the observation of suppression of Y would "strongly imply"

deconfinement. This is a funny expression: admitting that such an

observation would imply deconfinement (which some people may not be

prepared to do), what's the use of the adverb "strongly"? Something

either does or does not imply something else, without degrees.

We agree that the use of "imply" does not need degrees, and we also

agree that some people might not be prepared to admit that such an

observation would imply deconfinement. We do think that such an

observation would carry substantial weight, so we have rephrased that

part to "An observation of suppression of Upsilon

production in heavy-ions relative to p+p would be a strong argument

in support of Debye screening and therefore of

deconfinement"

We thank the referee for the care in reading the manuscript and for all

the suggestions.

> I think the paper is now much improved. However,

> there is still one point (# 2) on which I would like to hear an

> explanation from the authors before approving the paper, and a

> couple of points (# 6 and 7) that I suggest the authors should

> still address.

> Main issues:

> 1) (errors on subtraction of continuum contribution)

> I think the way this is now treated in the paper is adequate

> 2) (where did the subtraction error go?)

> I also agree that the best way to estimate the error is

> to perform the fit, as is now explicitly discussed in the paper.

> Still, I am surprised, that the additional error introduced by

> the subtraction of the continuum appears to be negligible

> (the error is still 20). In the first version of the paper there

> was a sentence – now removed – stating that the uncertainty

> on the subtraction of the continuum contribution was one

> of the main sources of systematic uncertainty!

> -> I would at least like to hear an explanation about

> what that sentence

> meant (four lines from the bottom of page 14)

Response:

Regarding the size of the error:

The referee is correct in observing that the error before

and after subtraction is 20, but it is important to note

that the percentage error is different. Using the numbers

from the single bin counting, we get

75.3 +/- 19.7 for the N+- - 2*sqrt(N++ * N--),

i.e. the like-sign subtracted unlike-sign signal. The purely

statistical uncertainty is 19.7/75.3 = 26%. When we perform

the fit, we obtain the component of this signal that is due

to Upsilons and the component that is due to the Drell-Yan and

b-bbar continuum, but as we discussed in our previous response,

the yields have an anti-correlation, and therefore there is no

reason why the error in the Upsilon yield should be larger in

magnitude than the error of the like-sign subtracted unlike-sign

signal. However, one must note that the _percent_ error does,

in fact, increase. The fit result for the upsilon yield alone

is 59.2 +\- 19.8, so the error is indeed the same as for the

like-sign subtracted unlike-sign signal, but the percent error

is now larger: 33%. In other words, the continuum subtraction

increases the percent error in the measurement, as it should.

Note that if we one had done the (incorrect) procedure of adding

errors in quadrature, using an error of 14.3 counts for the

continuum yield and an error of 19.7 counts for the

background-subtracted unlike-sign signal, the error on the

Upsilon yield would be 24 counts. This is a relative error of 40%, which

is larger than the 33% we quote. This illustrates the effect

of the anti-correlation.

Regarding the removal of the sentence about the continuum

subtraction contribution to the systematic uncertainty:

During this discussion of the continuum subtraction and

the estimation of the errors, we decided to remove the

sentence because, as we now state in the paper, the continuum

subtraction uncertainty done via the fit is currently

dominated by the statistical error bars of the data in Fig. 11,

and is therefore not a systematic uncertainty. A systematic

uncertainty in the continuum subtraction would be estimated,

for example, by studying the effect on the Upsilon yield that

a change from the Leading-Order PYTHIA b-bbar spectrum we use

to a NLO b-bbar spectrum, or to a different Drell-Yan parameterization.

As discussed in the response to point 6), a complete

removal of the b-bbar spectrum, a situation allowed by the fit provided

the Drell-Yan yield is increased, produces a negligible

change in the Upsilon yield. Hence, systematic variations

in the continuum do not currently produce observable changes

in the Upsilon yield. Varying the continuum yield

of a given model within the statistical error bars does, and

this uncertainty is therefore statisitcal. Therefore, we removed the

sentence stating that the continuum subtraction is one

of the dominant sources of systematic uncertainty because

in the reexamination of that uncertainty triggered by the

referee's comments, we concluded that it is more appropriate

to consider it as statistical, not systematic, in nature.

We have thus replaced that sentence, and in its stead

describe the uncertainty in the cross

section as "stat. + fit", to draw attention to the fact that

this uncertainty includes the continuum subtraction uncertainty

obtained from the fit to the data. The statements in the paper

in this respect read (page 14, left column):

It should be noted that

with the statistics of the present analysis, we find that the

allowed range of variation of the continuum yield in the fit is

still dominated by the statistical error bars of the invariant mass

distribution, and so the size of the 33% uncertainty is mainly

statistical in nature. However, we prefer to denote

the uncertainty as “stat. + fit” to clarify that it includes the estimate of the anticorrelation

between the Upsilon and continuum yields obtained

by the fitting method. A systematic uncertainty due to

the continuum subtraction can be estimated by varying

the model used to produce the continuum contribution

from b-¯b. These variations produce a negligible change in

the extracted yield with the current statistics.

We have added our response to point 6) (b-bbar correlation systematics)

to this part of the paper, as it pertains to this point.

> Other issues:

> 3) (two sigma effect)

> OK

> 4) (Trigger II cuts)

> OK

> 5) (embedding)

> OK

> 6) (b-bbar correlation)

> I suggest adding in the paper a comment along the lines of what

> you say in your reply

> 7) (trigger response simulation)

> I suggest saying so explicitly in the paper

Both responses have been added to the text of the paper.

See page 13, end of col. 1, (point 7) and page 14, second column (point 6).

> Less important points:

> 8) (repetition)

> OK

> 9) (Table I vs Table IV)

> OK…

> 10) (% in last line of Table IV)

> OK

> 11) (“strongly imply”)

> OK

We thank the referee for the care in reading the manuscript, and look forward to

converging on these last items.