The reviewers view on the first version of the paper was, for two referees (1 and 3), publish after minor revision and, for the third referee (2), reject. You provided a revised version of the paper responding to the referees’ comments and I, bearing in mind the verdicts on the first version of the paper, sent it only to the referee (2) who had recommended reject. That referee has provided further comments and has essentially not moved away from ‘reject’ recommendation.

Given this disagreement between the referees, and having read the paper carefully myself, my inclination is to go with the majority view and, in due course, accept the paper. However I think that referee 2 made some good points in their original review and not all of them have been answered convincingly. Also from my own reading of the paper I believe that the presentation can be improved significantly.

So I request that you submit a revised version of the paper, plus appropriate replies, that address the following comments of Referee 2 in particular, and also my own comments which follow. I will then consider it again myself (and would hope to accept it for publication).

Issues raised by Referee 2:

1) The choice to look at 10-year trends: I have some sympathy with the view of referee 2 here. It seems that you have chosen, within your simulations from 1960 to 2100, to focus only on trends certain 10-year periods within each simulation (during which changes in particular external drivers are somewhat similar to those over the observed 2002-2012 period). Referee 2 takes the view that this analysis is fragile because of the sensitivity of inferred trends to details of the time series at the beginning and end of the 10-year periods (or correspondingly, sensitivity to the precise choice of the end points of the 10-year period). You have answered this by saying that you have carried out longer integrations — but the fact is that you are still apparently focusing on a small number of 10—year periods. My own take on this is that, in using information only from a small number of 10-year periods you are discarding a lot of potentially useful information from your simulations. Have you not considered some other approach, such as, in the spirit of Dessler et al (2014), extracting correlation coefficients (between temperatures and the various drivers) over the whole length of the simulation and then considering the implied change of temperature over a particular 10-year period (given changes in the various drivers over that period).

2) The deduced effect of increasing GHGs or warming SSTs: You claim in your reply that you are unaware of a well-known long-term predicted increase of tropopause temperatures due to increasing GHGs. I am a little surprised at you saying that, but I agree that the story is complicated. For example, the Kim et al (2013) paper makes the statement in the abstract: in the RCP 8.5 scenario, the models predict robust warming both at the 100 hPa and
ZLR [= temperature minimum] levels, but cooling at the 70 hPa level. One of the problems with your paper is that you choose a single measure of TTL temperature which, I think, is the average over tropical box extending from 16km to 20km — so that averages over the warming in the lower part of that height range and the cooling in the upper part of that height range. In the average the cooling dominates slightly — and you make the statement that there is a weak average cooling trend — but you need to explain more carefully how this relates to previous work and how therefore, perhaps, there is no contradiction. (In your reply to referee 2 you show a time series of ‘tropopause temperature’ — but by what definition?]

My own comments:

p3 l19: ‘This recent warming of the TTL is different to previous reported temperature evolutions over the last decades’. Is it? Look at Fueglistaler et al (2013) Fig 4, for example — is 2002-2012 really so unique? To me this is simply interesting interdecadal variability.

p3 l23: ‘which might indicate a climate shift’, see comment above, this statement re a ‘climate shift’ seems amateurish and unnecessary. What do you mean by a ‘climate shift’ in any case?

p9 2.4: I’m not sure I understand how you calculate this composite trend — e.g. I find it difficult to interpret (5). More detail would be helpful (enough to allow the reader to repeat the calculation for her/himself). More importantly, perhaps, I don’t understand how the differing magnitudes in the change in the driver over different 10-year periods are taken into account. (For example, in Fig 1a the magnitude in the change in the ‘Total solar irradiance’ is different in each of the chosen 10-year periods — how does that get taken account in generating Figure 3?) If the differences in magnitude are ignored then you should say that explicitly and justify.

p10 l14: (also Figure 1) I think that you are saying that in order to calculate solar-cycle associated trends you have picked out 4 10-year periods — and these are indicated in Figure 1a. My comment is that they could be indicated much more clearly (and this applies even more strongly to other panels of Figure 1 where the straight lines corresponding to chosen 10-year periods are almost invisible). I suggest you put in vertical lines at the beginning and end of each 10-year period.

p11 l12: ‘The time periods of increasing QBO amplitude are selected by the same as the procedure as for the tropical SSTs’ — more detail would be welcome.

p12 l16: ‘Please note’ — omit ‘please’

p12 l18: ‘seed’ > ‘see’

p13 l9: You are deducing the ‘contribution of solar variability’ from the difference plot in Figure 3c — but is it not important in some way that the vertical structure in that plot is very different to the vertical structure seen in Figure 2, for example?

p14 l18: ‘zero-line just above the tropopause’ — actually I’d say that that zero-line is not far from the middle of your 16-20km region.

p16 l25-27: ‘This strengthened tropical upwelling cannot continue further up because of the westerly wind anomalies blocking transport into the subtropics and finally diminishing’ — I don’t see the justification for this statement — is there some dynamical reasoning behind it?

p17 l16: ‘slows down the transition branch of the BDC’ — ‘transition branch’ is a non-standard term — what do you mean?

p19 l16: ‘The QBO may influence the TTL temperature by modifying the BDC’. Actually my reading of Kawatani and Hamilton (2013) is that they are suggesting that changes in the BDC cause changes in the QBO. Are you deliberately intending to suggest the opposite and if so, why?

Fueglistaler, S., et al. (2013), The relation between atmospheric humidity and temperature trends for stratospheric water, J. Geophys. Res.
Atmos., 118, 1052–1074, doi:10.1002/jgrd.50157

Dessler, A. E., et al (2014), Variations of stratospheric water vapor over the past three decades, J. Geophys. Res. Atmos., 119, 12,588–12,598, doi:10.1002/2014JD021712.

I think that the changes you have made in this revision are helpful and I am pleased to accept the paper.

Two minor comments that you may wish to address before publication:

(i) Abstract l2 -- 'an unexpected warming' -- why 'unexpected'? You might think it is unexpected but someone else might not. It seems to me that variations in tropical tropopause temperatures over the last 25 years or so have simply shown significant variations on inter annual timescales of from 2-10 years. But this is not a very substantial point!

(ii) Perhaps more substantial -- when I first read your paper I was a bit confused about the nature of the QBO-associated variations. I had the impression that these might be associated with some subtle measure of the long-term variation of the QBO. But in fact it is now clearer to me that what you are identifying is the QBO signal in temperatures that has been known for a long time. The fact that the 'state' of the QBO is different at the end of some multi-year period compared to the beginning then implies a corresponding temperature difference. My suggestion is that you check your text to make sure that is as clear as possible.