Dear Dr Aschmann,

Unfortunately I received only one review for the revised version of your manuscript. I feel that you have not always responded to the reviewers’ comments with sufficient rigor. For this reason I provide herewith an editor review of the revised version of your manuscript. I provide my comments in the order of appearance in the manuscript, and point out for each comment if I consider it major or minor. Besides my review, please consider also the review provided by referee # 1, and consider re-submission of a revised version of your manuscript.

Sincerely,
Gabriele Stiller

Editor review of manuscript acp-2014-218, revised version, by Aschmann et al.

Abstract, l14-18 (major comment): In the light of Fig. 2, and in accordance with referee #3's comments, this statement seems to be too strong. The deviations of the trends derived from models and observations, respectively, and in particular in the early phase of the analysis period, seem not to allow to state that the model "reproduces" the observed records; the model is similar in the sign of trends, at best. I realize that the deviations and their potential causes are discussed later-on in the body of the paper (although this discussion remains rather vague). Nevertheless, this discussion does not justify such a strong statement in the abstract.

Footnote on page 2, 1st col (minor comment): I do not see the need for this footnote. This work can be referenced in the regular way.

Page 4, l87-91 (major comment): This is one of my most major and also general comments: The trend derived within this work from the combination of SAGE-II and SCIAMACHY after 2002 is about 0.5 % per decade, while the trend presented by Gebhardt et al. (2014) from SCIAMACY alone after 2004 is about 4% per decade. This is an order of magnitude difference. You earlier state that SAGE-II and SCIAMACHY fit very well, i.e. this cannot be the reason for the different trends. The only remaining reason is the slightly different period (2002 in your case, 2004 in Gebhardt et al.’s case). When looking into the time series of Fig 2., one might have the impression that the increase became considerably steeper after 2004. This puts into doubt if the turnaround point derived from the model time series is appropriately to be applied to the observations, or if the assessment of the turnaround point should not be done for each individual time series as presented in Fig. 3.

Said all this, I would like to clearly state that it is not the duty of the reader or the editor to find out why the trend numbers, published within 6 months in the same journal by the same research group with overlapping author lists, differ by a factor of ten. Instead it is the duty of the authors to give a satisfying explanation why the numbers published here at not in accordance at all (not even within 2 sigma!) with numbers published slightly earlier. Please provide a careful analysis (and not only some hand-waving arguments) on the discrepancy between your trend estimate and that of Gebhardt et al.

Page 5, l8 to end of section (major comment): Change of ODS is not the only process relevant for extra-tropical ozone variability, in particular in the UTLS; pollution transported to the UTLS and affecting the ozone budget there seems to be another source of variability with at least similar importance. For this reason I don’t right see how the sensitivity studies related to ODS emissions could help to analyze the impact of in-mixing of ozone into the tropical LS.

Page 5, l33-35 (minor comment): This is not necessarily a contradiction; shift of the mixing barriers may show up as a reduced tropical upwelling if the latitude band under analysis is not shifted accordingly.

Page 5, l53-63 (major comment): The discussion of the weaknesses of the EI heating rates remains rather vague, given that this was a major point in the comments of reviewer#3, and no attempt is made to provide a quantitative assessment of the errors introduced by this. Could you give an estimate, or is there any reference in the literature, what the magnitude of the overestimation of the upwelling in the tropics is, and how it changes with altitude and, most importantly, with time? Which period is represented best by the fixed ozone climatology used within EI? Why do you assume that the discrepancies between the model and the SAGE-II data are due to these shortcomings, and why should only this period be affected? Do you have any indication for this assumption?

Figs. 3 and 4 (major comment): Please provide the trends shown in panels b, d, and f (Fig. 3) and b and d (Fig. 4) additionally as numbers (i.e. values of w_1 and w_2 or w) in a legend so that the reader has a chance to compare the derived trends for the various data records.

Page 7, l14-21 (major comment): The different signs for the mass flux trends in and out of the shallow branch indicate some kind of a divergence before 2002 and convergence after 2002. These source and sink terms need to be compensated for, for example by decreasing (before 2002) and increasing (after 2002) pseudo-horizontal transport, which in turn, should affect the strength of in- and out-mixing into/from the tropical pipe. How does this, in turn, affect tropical LS ozone and its trends? This question is also related to one of the major concerns of reviewer # 1 which has, to my opinion, not been properly addressed.

Page 8, l17-21 (major comment): Given what has been shown on Page 7, lines 15ff, I would expect the blue line in Fig.7 to change from correlation to anti-correlation (or vice versa) around 70 hPa (~ 19 km) since the trends in the mass fluxes for the transition and the shallow branch have always differing signs. However, the w* is always positively correlated with the surface temperature. Any explanation for this?

Conclusion (major comment): I miss in the conclusion completely the discussion of the role of mixing processes; in particular, since the paper gives indirect evidence (see my comment to page 7, l14-21) that mixing with the extra-tropics must have changed considerably during the period analyzed, and, moreover, at the same turnaround points as the trend change in ozone. Change of ozone trends due to change in the strength of mixing cannot be excluded in the first place, and the conclusions need to discuss why this work has provided evidence that change in mixing strength is not the driver for ozone trend changes.

Dear colleagues,

about two weeks ago I was asked to take over this manuscript as the Editor, which I have done later (Oct 9). In the meantime I have checked in detail the correspondence between the former editor, the referees and the authors; and in particular, I have carefully read the revised manuscript (version of August 28).

From my point of view the paper (as is!) should be published. Mostly all comments and suggestions raised by the referees have been adequately considered and also the specific points raised by the first editor have been taken into account in the last revision of the paper.

Martin Dameris