Dear Dr. Ming et al.,
You are encouraged to revise the manuscript by addressing further important comments and suggestions from the 2nd reviewer (see below). Please particularly clarify the potential role of clouds, how the model’s 2-D representation performs, the potential differences ‘arising from implementation rather than dynamical adjustment’, and the uncertainties in the ozone data used in the tropics and the sources.
Best, Qiang Fu

Review of the revised paper by Ming et al

General comments on the response document and revised manuscript.

1) In the response document, there are now statements about the IGCM calculation having potential differences ‘arising from implementation rather than dynamical adjustment’. This was not mentioned in the original manuscript. What causes potential differences in ‘implementation’? Does this remain a potential source of error in the revised draft, and how well quantified is it?

2) In the response document and in the manuscript, it is stated that since the results reproduce the annual cycle then the net effect of clouds must be small. The response document refers to ‘rough quantitative estimates’ to back this up, but that is quite loose language. How rough? How quantitative? It is later stated that no results regarding this concern will be given in the draft because ‘the problem is sufficiently complicated that a brief explanation could not do it justice and the scientific uncertainties are large’. So the reviewer is first presented with an assertion that the effect of clouds must be a small one (because the seasonal cycle looks good without it), and second a statement that the uncertainties are large. This is not an appropriate response. Getting the ‘right’ answer for the annual cycle can happen for wrong reasons, and the assertion that clouds are not important even though uncertainties are large is speculation. Particularly given the potential for cloud feedbacks in a dynamical calculation to affect radiation (e.g., through changes in cirrus in regions of altered upwelling, although that is only one example among many), I think further information is required beyond the statements made that this is ‘beyond the scope of this work’. The paper needs to be revised to address this more clearly.

3) I did not find the author’s response to my question 7) to be sufficient. I am asking about the mean meridional circulation in this representation of the model (as implemented, which could differ from other uses of the IGCM that may be discussed in the literature). Since the paper seeks to calculate thermal responses associated with imposed constituent changes, it seems to me to be quite important to determine whether or not the mean meridional circulation that is found in this representation of the model prior to imposing the perturbation is accurate. One approach that can be used is tracer transport tests, for example. I don’t find the statement in the paper regarding the difference of 2K from a control run in the tropical stratosphere to be proof that the reader should be confident that an accurate balance exists in this representation of the IGCM model between radiation and vertical motion near the tropical tropopause. Both of these terms are known to be important drivers of temperature seasonal cycles in the region of interest, and 2K would be a very important change if it occurs close to the tropical tropopause. A 4 year long ‘control run’ is carried out and results for the perturbed versus control are shown for a 5th year, but the rationale for a 4-year control is not given when it is introduced, and there is no discussion of how the model behaves over the ‘spin-up’ period in this configuration compared to IGCM 3.1. If the spin-up produces a mean circulation that is not realistic, and differs from the parent IGCM, that raises concerns about the experimental design. My concern here has to do with more clarity on how the model’s 2-D representation performs, particularly given the focus on specific latitudinal structures that are highlighted. These may well be correct, but the paper needs more clarity on its underlying methodology.
4) I appreciate the added appendix C but remain concerned about the discussion of uncertainties in SWOOSH ozone, and the authors’ response to my criticism. The authors use the interannual standard deviation of SWOOSH values in providing tests in Appendix C. But the variability from year to year is not a measure of absolute accuracy. This should be explicitly stated. Further, the authors quote Tummon et al. (page 29, line 30) regarding the spread among satellites in the lower stratosphere. But it is clear that the uncertainties in the region of interest here, the lowermost stratosphere in the tropics, are considerably greater than global average uncertainties, in part because ozone is so much less abundant in the tropical lower stratosphere than globally. In the response to my comment, the authors assert an uncertainty of 10% at 70 hPa and 30-40% by 130 hPa and refer to Davis et al. I could find no such statement for the tropics in the Davis et al. paper. Again, I request the authors to clarify where specifically this estimate comes from, whether it is a value for the tropics or simply a global average and therefore probably too generous in the tropics. Please give uncertainties appropriate to tropical latitudes and say where they came from.

Further comments in addition to the above:

5) page 5 and elsewhere. Temperatures are taken from ERA for 1991-2010, but ozone and water vapor from SWOOSH are for 1984-2015. Why the inconsistency? Why not use 1991-2010 from SWOOSH?
6) Page 5, lines 28-31. The assertion that reproducing the annual cycle means cloud effects must be small should be removed for the reasons discussed above.
7) page 6, line 12. What is meant by ‘accurate convergence’ and how was this determined? Loose language detracts from the paper in several places; this is an example but I suggest that the authors try to tighten up throughout.
8) page 8, line 12-16. I think 10% is far smaller than can be defended as a 2-sigma absolute (not interannual) uncertainty for tropical lower stratospheric ozone. This sentence is not useful or needed, just delete it.
9) page 8, line 23. You quote 60% from one region and 30% from another. Where is the remaining 10%? Is there a 40% total contribution when additional higher levels are considered?
10) Pages 6-10. The paper uses loose and inconsistent language in deciding when there is a ‘significant’ non-local contribution for water vapor versus ozone. In the case of water vapor, on page 10, line 7, an 0.4K non-local contribution for water vapor out of 1.1K (i.e., 36%) is deemed ‘significant’, while on page 8, line 22, a 30% contribution from ozone from higher altitudes is simply dismissed (with 10% unaccounted for), and it is stated here and elsewhere that the ozone response is primarily local. Please do account for the missing 10% by examining your calculations rather than leaving this hanging. In any case, even without the extra 10%, it looks to me like the two are comparable, and this should be stated. I suggest that the word ‘significant’ may be best reserved for things tested statistically, not those where the author’s view is expressed. The paper should avoid loose judgments on what is ‘significant’ and what is not, and make consistent comparisons throughout. The question of non-local effects for both ozone and water vapor comes up in several other places in the paper, and needs consistent propagation in all its places of occurrence.
11) Page 11, line 6. You don’t compare your findings regarding non-local effects to Gilford and Solomon. That should be done here, since it was a key focus of that paper.
12) Page 14, lines 9-13. This statement first critiques Randel, then speculates as to why his results may differ, then admits to substantial uncertainties underlying that criticism. Avoid loose speculation in critiquing other work, delete this.
13) Page 15 and elsewhere. This section is interesting, but the paper is too vague regarding the outcome. What is the origin of the implied “upper tropospheric constraint”? Could it be clouds? Something else? Are there any insights to be had from the full IGCM? This isn’t very useful unless it can at least clarify what may be meant here.
14) page 22, lines 23-26. Ozone values are stated for 70 hPa, while H2O values are stated for 90 hPa. Consistent comparisons should be made. Page 8, lines 21-24 state that 30% of the ozone effect at 90 mbar is non-local, (perhaps 40%, when the missing 10% is accounted for). Therefore, at 90 hPa your results suggest similar magnitudes for non-local effects of both species.
15) Please comment on the differences between Fig 1 (ERA-interim) and the combined effects of ozone and water in the IGCM shown in Fig 12. Do the residuals seem plausible? What do you think accounts for them? At 90 hPa in particular, there seem to be some large remaining terms if this model is correct. What do you think they could be?