In response to your request for comments, here are mine:
> >1. The authors begin by introducing the expected P(f) for a DCC state. It
> >would be good if they could present the distribution they have found, or
> >at least one that is consistent with their data. Can they not unfold this
> >distribution? Is the neutral pion fraction indeed 1/3?
I am afraid the referee is confusing the distribution, P(f), with the
average distribution of neutral to total pions. We can certainly present
a distribution that is consistent with our data: P(f) = a delta function
of (f - fo) where fo is any constant between zero and one. We could add
a sentence or two to the sixth paragraph of section VI. CONCLUSIONS.
"The values of the robust observables calculated from our data are
consistent with the ratio of neutral to total pions being governed by a
binomial distribution. While we made no attempt to extract the actual
distribution of neutral and charged pions, our data show that, at the
ten percent level, our results are consistemt with events generated by
> >2. The authors should clarify a seeming discrepancy regarding event
> >rates. They state (on page 6) that their trigger cross-section was 43 mb.
> >The lowest luminosity they appear to have run at for the 6 day run seems
> >to be of order 10**28 /cm**2/sec. This would imply a trigger rate of 430
> >Hz so that they could collect all their 1.3M events is less than one hour.
> >Even given modest dead-times, I don't see how they could have taken 6 days
> >worth of data. The reported trigger rates don't seem to make sense either.
Good point. There is an error in the paper where we say, "The
luminosities during these runs ranged from ~ 10^28 cm^-2 s^-1 to ~ 10^30
cm^-2 s^-1." Referring to Table 2.10 of Mary's thesis one can see that
the numbers we quote are D0 luminosity. I would suggest the following
sentences be substituted for the above: "The luminosity at the C0
collision point was inferred from the D0 luminosity corrected for
differences in the magnetic architecture at the two points and the fact
that bunches that collide at C0 are not the same pairs that collide at
D0. The C0 luminosity ranged from about 10^26 cm^-2 s^-1 to 10^24 cm^-2
s^-1". But Mary or someone should check these numbers before making that
change. I am slightly confused by the last paragraph in section 2.2.3 of
her thesis. What was the correction for different pairs colliding?
> >3. A concern remains with this reader about how valid the results are,
> >given that they have trouble simulating their backgrounds. Have they made
> >any attempt at superposing additional hits on their simulated events and
> >then testing whether their novel statistics change significantly? As I
> >understand it, after cuts their simulation reproduces track and photon
> >distributions [see comment 8 below] but it fails to reproduce lots of
> >extra hits away from tracks. True? (If so, this is not uncommon or
The "this is not uncommon or unexpected" comment is interesting. To me,
this is the most troubling criticism of the paper. I recall having
discussed the idea of throwing extra hits into the simulated data at one
of our collaboration meetings. I don't recall if it was ever attempted.
Mary can throw some light on that, I hope.
> >4. I don't understand the statement on page 14 that the deviations from
> >unity for the higher order ratios in Table VII are not very significant.
> >The reported values are FAR more significantly different from 1.0, using
> >the quoted errors, than are those for the low order ratios. Perhaps when
> >normalized to their monte-carlo, this effect goes away but the authors
> >give no indication of that.
Perhaps by the phrase "The higher order ratios", the referee thought we
meant r(0,2), r(1,2), etc., which are, indeed, far more significantly
different from 1.0. I would suggest the following for the third and
fourth sentences of section V A:
"The values of r(1,1) are close to what is expected for a binomial
distribution. The values of r(i,1) for i>1 are more influenced by bins
of N(nch,ngamma) that are statistically limited and therefore the
deviations from unity are not as significant." Then some remark ought to
be made about r(0,2), etc. (such as they depend on knowing gamma
detection efficiencies?) or those entries eliminated from the table.
> >5. The authors claim that the low-order ratios for diffractive and
> >forward tagged events are consistent with those from the total sample. Yet
> >in every case, the numbers are greater in these samples than in the total
> >sample; and this tendency continues for the higher order ratios as well.
True but not significant as the numbers in a given column of table VII
are not statistically independent. Perhaps a statement to that effect
should be put in the caption to the table.
> >And by the way, does the simulation give the correct fractions of events
> >for these tagged samples?
Did the GEANT calculations include all that downstream stuff to the
kicker magnets, etc.? I assume not. Somewhere under section III B a
statement as to what hardware was included in the simulation should be
> >6. At the bottom of table VII are found the values for the low order
> >ratios using the alternative tracker. The event total just above the
> >bottom three entries seems to be those found with the alternative tracker.
> >If so, this should be stated somewhere; and then it needs to be explained
> >why this tracker seems to be only 18% as efficient as the nominal one.
> >This is doubly puzzling in that the other subsamples that are called out
> >(diffractive, forward) have comparable event totals for the two trackers.
That's easy. In the caption to the table we should add a sentence, "#
events refers to the number of raw events put through the respective
> >7. The technique of using ratios of factorial moments seems to allow
> >extraction of the physics without the need to worry about things such as
> >tracking efficiency, etc. But what information is lost? I.e., if one did
> >fully understand efficiencies, could more be learned?
Of course. I don't know what to do about this one.
> >8. I don't understand what conclusions are to be drawn from Figure 8.
> >Is it that the simulation gets the normalization and distribution of
> >charged and neutral particles correct at the 10% level? This would follow
> >if the simulations include detector effects which they no doubt do. If
> >so, the authors should state this as it gives important validation of
> >their simulation procedure and of their understanding of their analysis
> >and cuts.
The caption to Figure 8 is a little confusing. How about: "FIG. 8 Raw
distributions of charged and neutral particles. The curve labelled
"PYTHIA" refers to simulated events produced by the PYTHIA event
generator. Also shown are the expected distributions after these events
are propagated through the GEANT detector simulation algorithm and the
observed distribution. The close agreement between the "DATA" and
"GEANT" curves validates the simulation procedure and our understanding
of the analysis and cuts." (The referee said it!)
> Also, the large shift between PYTHIA and GEANT for the photon
> >distribution, no doubt having much to do with conversion probability,
> >should be explained in the caption (or in the text).
> >9. Finally, there is no clue as to why the experiment is called
If the Phys Rev editors want to put up with an explanation, why not.
Two minor points: The second sentence in section III A has an upside
down ? preceeding it in my copy. Bob Leskovec's middle initial is A, not