All three referees have given comments on the revised version of your paper. Two now recommend publication (one after minor revision). The third continues to have significant reservations about aspects of the paper and has set out those reservations in a carefully written detailed report.

Please consider further revision in the light of the latest referees comments and provide a revised version of the paper plus responses to the comments of referee 3 (which are substantial) and referee 1 (which are minor). I will look carefully at your revised paper and the responses myself. Ideally I will be able to accept the paper without requesting a further opinion from referee 3 -- but whether I feel I can do this depends on the revisions you make and on the responses.

The referee to whom I sent the latest revision of your paper continues to have reservations about whether it is suitable for publication. The referee is particularly concerned about three aspects of the underlying assumptions of the work, as described in items 1-3 in their report.

The referee has put significant time into considering this paper and I think it is time to relieve them of responsibility. The other two referees recommended publication and I will go with the majority verdict and accept the paper, provided that some suitable changes are made to the text to acknowledge the concerns of the remaining referee.

My interpretation of these points raised by the referee are as follows. In cases (1) and (2) I have proposed some straightforward (and, I think, justifiable) changes.

(1) The GW contribution as defined is actually a contribution from 'unresolved' waves and the 'resolved' waves may include a contribution from GWs. The referee suggests that the resolved waves are divided into RW and GW contributions on the basis of zonal wavenumber. A simply alternative alternative would be for you to make it absolutely clear at key points in the paper (abstract, introductory sections, conclusions) that your distinction is between resolved and unresolved waves and that the resolved waves may contain some gravity waves.

(2) The residual in the momentum equation (and the corresponding contribution to the mass stream function) cannot be reliably interpreted as the GW (or unresolved wave) contribution since the assimilation increment, which contributes to the residual, is influenced by many different aspects of model error against observation. Your argument against that is that many of the characteristics of the GW contribution that you identify are common to all four reanalysis datasets. The differences between the datasets are quite difficult to identify from figures such as Figure 2. Quantitative comparison is easier in Figures 3-5, where it is clear that estimates of the GW contribution differ by up to a factor of 2. Therefore, again at important points of the paper, please emphasise that whilst there is qualitative agreement between the results from the different reanalyses, there is significant quantitative uncertainty (as illustrated by Figure 3-5). Your current statement on l28 p19 'First the results from the four reanalysis [datasets] were quite similar except for minor features' -- for example -- seems much too strong. (A factor of 2 disagreement is not minor.)

(3) I'm not completely clear on this point. Certainly Geller et al (2013) seem to imply that GM momentum flux is significantly overestimated by parametrizations compared to observations -- 'The faster fall off with height of the gravity wave momentum fluxes derived from satellite measurements than in models is the most severe disagreement between measured and model fluxes shown in this paper.' -- though you have argued against this in a previous response. (Perhaps you were arguing specifically against the suggestion that the disagreement was caused by 'tuning' of the parametrisation?) But it is not clear to me why that implies you are overestimating the GW contribution -- unless the inclusion of the GW parametrization in the model has an effect on the assimilation as a whole (more than simply changing the assimilation increment -- e.g. if it somehow affected the estimate of the RW contribution). Please consider once again whether this general point requires any change -- e.g. addition of a sentence indicating uncertainty.

Given that I am going to accept the paper in a situation where a referee still has significant doubts, I have looked again myself at the paper as a whole and have noted the points below. Please make changes to address these (there may be other typographical errors that I haven't spotted) -- or provide brief justification why no change is needed.

p1 l8: 'data' > 'datasets'

p3 l21: 'hardly' doesn't make sense -- 'poorly'?

p4 l21: 'Randel (2008), as described above' -- wasn't clear to me what your 'as described above' referred to -- be more specific. I think that this is your 'second' method on p3.

p4 l30: Your use of 'potential' here represents an important definition (which would not be clear, for example, to someone reading the abstract -- who would not know that 'potential' was being used in a certain sense).

p4 l32: This justification of a broader use of 'potential' is very confusing. The first use is required because of dynamics (the response to a force is both an acceleration and a meridional circulation). This is completely distinct from uncertainty due to mismatch between model and data.

p7 l14: 'function by' > 'function driven by'

p8 l8: 'However, the similarity among Psi_GW (phi,z) estimated ... from the four reanalysis datasets ... MUST show real dynamics' -- it is this sort of statement that I think continues to trouble the referee -- their comment (2). I could, imagine, for example, that the time and space sampling of the data used (which is presumably pretty much the same for each of the re-analyses) relative to the high (and regular) space-time resolution of each of the models being used for the reanalysis leads to a significant contribution to the data assimilation increment that is common to all the models.

p8 l31: 'the zonal mean zonal wind tendency term ... is evaluated as the radiation effect' -- personally I'd question whether this term can reliably be associated with radiation alone, but if you want to make this working assumption then it is important that your introduction of the term 'radiation effect' is presented to the reader here as a definition -- and that definition is properly referred to later -- e.g. on p19 l19 you use the term 'RW and radiation contributions' and the reader needs to be reminded that you have a particular justification for using the term 'radiation contribution'. Again -- personally if I were writing your paper I would continue use 'pa u/pa t contribution', because that relates directly to what you have calculated, rather than requiring an extra assumption about the physics.

p9 l16-18: You should give more details on the levels in the models. (These details are surely as important as those on horizontal resolution, which you do give.)

p17 l28: Geller et al 2013 is cited here, but as far as I can tell is not included in the reference list.

Appendix A: This doesn't necessarily require action on your part, but I find some of your statements in this Appendix puzzling. You are noting that using a vertical integration of vbarstar vs a horizontal integration of wbarstar to deduce Psi can give different answers. You are taking vbarstar and wbarstar from the re-analysis dataset. To me the difference between the two calculations potentially arises from a combination of non-zero divergence of the (vbar,wbar) field, or from inconsistency between the numerical integration/differentiation that you are using in your calculation vs that which is used in the reanalysis calculations. I don't see how you draw any conclusions about e.g. the role of wave forcing in the stratosphere/mesosphere (l25-29 on p21) or with the existence of GW forcing in the mesosphere (l30 p21 - l3 p22).

I am pleased to accept the current version of the paper for publication in ACP.