The authors wish to thank the reviewer for the prompt and careful consideration of our manuscript. We have made modifications to the paper as indicated (with additional commentary) below. > This manuscript should be published after the authors have made some > changes and after they have considered some improvements to the > manuscript. The work is a valuable contribution to neutrino physics > measuring the Q2 distribution of quasi-elastic events on nuclei. > Could the authors replace all occurrences of the abbreviation > Tab. with Table? Done. > I find the title very misleading. Almost 22% of the interactions are > on aluminum and the fact that the target contains oxygen is of only > marginal significance. The first line of section IIA, formula 1 and > equation 5 assume the reaction is with a single (bound) nucleon, a > neutron to be precise. The title is chosen to be both concise and expressive. Here are some alternatives that are less preferred: "...neutrino-nuclei interactions" does this include H? D? Fe? "...neutrino-neutron interactions" ignores the nuclear contribution? "...neutrino-heavy nuclei interactions" but heavy relative to what? "...neutrino interactions with oxygen and aluminum" might be okay. Regarding the difference between oxygen and aluminum, we estimate that despite the uncertainty in the size of the nuclear effects, aluminum is much more similar to oxygen than either are to deuterium or free neutrons (or iron, to name another detector material in use today). The correction for aluminum compared to oxygen, on the per neutron basis used in this analysis is not 22%, but an order of magnitude smaller. In other words, we think neutrino-oxygen has the advantage of being concise and expressive. To the extent that there is aluminum content, the relative effect is in fact small and discussed in the manuscript. > The authors must do a better job to justify their result since it > their value of Ma is substantially larger than previous work in > the field (table 6). This is also related to the specific comment the reviewer gives later. See our reply there. > More specific comments follow: > The data in table I seems to be confused. The MC was to be normalized > to the data sample. For the K2K-I data these differ by 2 events, > which could be round off to integers but the K2K-IIa samples differ > by 28 events. How is the MC normalized? Fixed. Typed in wrong number. The correct number in the data column is 3623, same as in Table III on the next page. Thank you for noting that. > Figure 5 does not seem to show a deficit of events with muon angle > near the beam as mentioned in the text. The solid line (MC > prediction?) seems to match the data at low angles fairly well. We have modified the text slightly to be more explicit about the deficit. Figures 5 and 6 are the same physical quantity plotted two different ways, except that Figure 5 has no CC coherent pion, while Figure 6 has MC predictions with and without CC Coh. Pi. So, with zero coherent pion, with the data spread through 0 < angle < 11 degrees, and with the combination of subsamples, there is no apparent discrepancy at low angle in Figure 5, as the reviewer correctly notes. The text refers to Figure 6 twice, indicating that there are physics reasons for a MC to have difficulty predicting data in the two highest bins in cos(theta). > In section IVB could the authors state clearly the number of Q2 bins > used in the fits. The text states that the high Q2 bin is adjusted > to contain at least 5 events. But the number of bins and the maximum > value of Q2 is not stated. This is a list of 30 values: the fit is to 5 energy ranges for each of three subsamples for each of two data sets -- each has a unique point in Q2 where all data above that point is summed into a single bin. We can, of course, easily supply such a list, but feel it would detract from the text, even if presented in the form of a table. But we understand how this information is useful, and have summarized an approximate range of values in one sentence added to the Fit Procedure section. > The caption on figure 7 was written for a different layout of the 6 > plots. on my copy there are 2 columns of three figures, three rows. > The caption speaks of two rows, top and bottom. Figure 6 also has > this caption problem; the third plot is below the other two. In > figure 6 the use of the term "top line" is ambiguous, since the > dashed and solid curves are both on top for some bins. The authors' preferred layout is two rows of three figures each. We will work with the editor to be sure it appears this way when the layout is finalized, or that the caption is changed appropriately. > The authors need to give a detailed description of how the nonQE part > of equation 8 is calculated. The fit is basically a fit to two shapes > the QE part parameterized by equation 1 and the nonQE part for which > there is no clear description. > I would welcome both a formula and a plot of this nonQE > distribution. (The plot would seem to be part of figure 7) > How does it differ from the QE distribution? What portion of > the data is most effective at distinguishing these two hypotheses? The nonQE part is not a simple formula. The implementation of the Rein-Sehgal and DIS components are the sum of several individual components -- 18 different resonances are included, then there is the DIS contribution, and a parameter (Bodek-Yang) which is used to adjust the overlap between these two. The nonQE background predicted by the MC is indicated by the white region in Fig. 7, though that figure is the results after fitting, so it is already adjusted by the nonQE factor 1.30, includes all detector effects and the adjusted energy spectrum. The most useful quantitative information for this measurement would be a comparison of the NEUT implementation with one or more of the competing neutrino event generators (Nuance, Neugen, Genie) utilizing identical beam spectra and detector acceptance configurations. Such comparisons have been published for other kinematic quantities, but not Q2. We have added a reference to one of these [Gallagher et al, from NuInt04]. Unfortunately, a similar comparison of either true or reconstructed Q2 is beyond the scope of this manuscript. The reply continues in response to two further questions below. > Does Table IV indicate that the non QE fraction is 1.3 times the > QE fraction? (Perhaps but it does depend on how NQE and NnonQE > are normalized). It indicates that the nonQE is 1.3 times nominal. We have improved the notation of this parameter, and instead write R_{nonQE} to indicate that it is a reweighting parameter and remove any hint that it is a ratio of something to something else. With this notation change, the manuscript's discussion of how this simple parameter accounts for several sources of uncertainty is more clear. > If one were use a NonQE Q2 distribution with a little more weight > above Q2 of 0.7 would this give a lower value for MA? Would this > be a poor representation of the NonQE component? How poor? > There are no parameters in the fit for the NonQE shape. > Only its normalization is fit. Why is the NonQE Q2 distribution > better known than the QE one being studied? We address these related questions in the opposite order. There are no parameters in the fit, but there are two parameters studied as additional systematic errors. The natural parameter with the largest effect on the shape of the nonQE background is MA-1pi. In Section V.B.4 we indicate that a 10% change in this produces a 3% change in MA. Another parameter, the size of the Bodek-Yang correction applied to the cross-section in the resonance-DIS overlap region has an even smaller effect. (A correction to the manuscript has been made. A 10% change in MA-1pi produces a -/+ 0.03 change in MA-QE: note the minus/plus rather than plus/minus. In other words, decrease MA-1pi from the nominal 1.10 we use to 1.00, the fit value for MA-QE will rise by approximately 0.03.) The NonQE Q2 distribution is not known better, but even without a joint fit, our analysis methodology indicates the uncertainty in the shape of the NonQE background from known sources contributes a small amount to the uncertainty in the shape of the QE portion. ---- About the first statement. > If one were use a NonQE Q2 distribution with a little more weight > above Q2 of 0.7 would this give a lower value for MA? Would this > be a poor representation of the NonQE component? How poor? The reviewer posits a particular scenario to adjust the shape of the Q2 distribution, which we address here in this comment. Increasing the weight of the nonQE above Q2 = 0.7 by 10% produces a fit value of 1.16. The best way to use the information in this manuscript to evaluate a particular systematic scenario is given in section V.D.5 and Fig. 10. If the scenario can be approximated by a change in slope in the bulk of the Q2 distribution, then a slope of of approximately 0.02(GeV/c)-2 in the QE Q2 distribution corresponds roughly to a change in MA of +/- 0.01. To apply this to the nonQE background makes roughly half the relevant samples, the same conversion factor applies, but with a minus sign. Reweighting everything above 0.7 a factor 1.10 higher is roughly a slope of 0.10, and would produce a shift of roughly MA -/+ 0.05, similar to what is obtained directly using our fit code. We have added a paragraph making this methodology clear. The reader is not able to evaluate goodness of fit in this way, but can consider alternate systematic scenarios. The reviewer also seems to ask "what would make the nonQE distribution fit better". The primary disagreement to the nonQE shape is that the distribution in the data seems to be steeper than in the MC. This can be modeled, following the procedure above, as a slope of -0.10 in the nonQE background (combined with an appropriate shift in normalization.) Forcing that to give better agreement using this ad-hoc method, without regard to a model, would shift the QE-MA fit value *up* by 0.05. An example of a model that could give such a shift is MA-1pi = 0.90 instead of 1.10. > One troubling feature of the result is the rather high value for MA. > Table 6 makes it clear that this high value is not due to the use of > newer vector form factors, since the use of the old vector form > factors gives an even larger value of MA. Previous measurements may > have had a much purer sample of quasi-elastic events. The authors of > this manuscript should study the stability as a function of the sample > purity. Figure 8 tries to do this. We can not significantly improve the purity with these data. As you note, we can change the value of the low Q2 cut and make a somewhat more pure sample as the value of this increases, as shown in Fig. 8. Also, we studied changing the value of the delta-theta cut used to divide the two-track samples. In this case we can not get more pure separation, but by increasing this value we can make the 2-tk QE sample LESS pure. We find that a wide range of values for this cut make no difference to the result of the fit. (MA +/- < 0.02 for a range between 15 and 35 degrees.) This effect was one of many we studied, found to be negligible, and did not put in the original manuscript. However, the reviewer is correct that the sample purity is one of the primary differences between our analysis and previous measurements, so we have added a comment about this to the "Comparison with other experiments" section. > There is something very funny about figure 8. The horizontal > "best fit" is below all the points except the one at Q2=0.2 > which it goes through. It is a combination of the correlation between these points which use the same data, and the systematic uncertainties are still free parameters. Constraining the systematic uncertainties to their best fit values would more closely produce the behavior you expected. > The text indicates that the fit value when no cut is applied is > 1.27+/-0.12 with 0.07 of this error being systematic. This gives > a statistical error for this point of 0.1, but the error bars plotted > are less than half this size? Are the points on this plot correct? We have modified this description. It more clearly indicates the 0.12 includes an additional 0.07 from the low q2 uncertainty. It happens to come out to 0.12 again, but in the case of this point, the total uncertainty without this addition is reduced from 0.12 to roughly 0.09 when the same error sources are included, but rises again when the additional 0.07 (in quadrature) is included. This reduction to 0.09 is the increased statistical power included in what we have called "statistics" and "normalization" parts of the analysis. > Again for figure 9 the best fit curve is above all points but the one > at 1.75 GeV. In this figure one assumes that the points are not > correlated. If the error bars of figure 9 have their customary > meaning a lower value for the combined fit would give a lower > chi square. These points are actually correlated also, because the fit does (must) include MC from neighboring Etrue regions. We have made this more explicit in the accompanying text. The text also indicates that there are different restrictions on the systematic effects that are relevant in this case. > In table 4, is the substantial error on the 0.5-1.0 GeV neutrino flux > understood? Yes. There is very little power to constrain this because, once the lowest q2 region is eliminated, there are only 12 bins of data included in the fit for these low energy parameters. > The classic cited at reference 1 is slightly in error. The author has a > hyphenated name. The citation should be to C. Llewellyn-Smith. We have tentatively made this change in our manuscript, however the original article cited does NOT include the hyphen. The PRD editor should give us advice about whether the author's preferred spelling or the citation's actual spelling is more important in this case. > The authors must do a better job to justify their result since it > their value of Ma is substantially larger than previous work in the > field (table 6). > In spite of a great many details about the experiment the reader is > left with the impression that the result is not well understood. Considering the size of the experimental uncertainty, this measurement can be considered "high but not inconsistent" with previous deuterium results. On the other hand, we would not say we have confirmed or validated these previous measurements -- we did not assume a-priori that the shape of the Q2 distribution should be the same for oxygen as it is for lighter nuclei. This was a significant focus of the analysis. We have improved the concluding paragraph to be something like this: "This result is higher than previous measurements, especially those on deuterium. We find the most significant sources of systematic error are experimental, and our results are different from deuterium measurements by about two standard deviations. We note that this analysis is very sensitive to the absolute muon momentum scale. We do not assume that neutrino interactions on oxygen should be the same as for deuterium; however, we find only a small effect on the shape of the $Q^2$ distribution for $Q^2 > 0.2$ (GeV/c)$^2$ from known nuclear effects." > > > Other changes The hep-ex preprint generated in inquiry from a review article author. We have made reference to this article in K2K internal technical notes in the past, and agree that a reference to that article has some relevance for the reader and is appropriate for this publication. We have added V. Bernard, et al. (2002) to the citation list. > > > In summary: Clarifying remarks added to five sections in response to reviewer's questions, couple typos fixed, and two new references.