Referees 1 and 2 were both strongly critical of the first version of this paper.

Referee 2 (Stephan Fueglistaler) has now considered the revised paper and his recommendation is that the paper now be accepted after minor revision. He sets out various detailed comments.

Referee 1, who recommended rejection of the paper in the first instance, does not have time for a detailed review of the revised version of the paper. Therefore I have decided to provide such a review myself, focusing on the points that were of particular concern to the Referee.

Referee 1 originally raised the following points:

1. Analysis is limited to temperature response and does not consider any effect of variation of pathways.

2. The discussion of the observed millennium drop is imprecise — for example there is vagueness about timing of a drop seen in simulations vs the timing see in the observational record.

3. Various terms are not precisely defined.

4. Greater precision is needed in the discussion of ‘nonlinearity’ and its possible relation to the 1997/98 El Nino event. Arguments for the importance of Indian Ocean surface temperature anomalies in the nonlinearity are poorly supported by evidence.

5. The discussion of the detailed predicted time variation of water vapour is poorly related to the observed record — for example there is a predicted significant drop in water vapour in 1997 but that is ignored in the discussion.

6. The reason for considering mean age is not made clear and the method for calculating mean age is not properly described.

Referee 1 also made a number of detailed comments, but emphasised that they had not provided an exhaustive list of recommended technical corrections because their overall recommendation was that the paper required a complete rewrite.

Having looked at your revised paper, my impression of your response to the above comments is as follows.

1. You have acknowledged that there is no consideration of the role of changing pathways in the determination of the water vapour response to El Nino, but in a rather indirect way which seems to suggest that variation in pathways might be responsible for variability between ensemble members rather than for systematic variation. My recommendation is that you make this acknowledgement more conspicuous and, unless you can justify the argument carefully, you remove the suggestion that variation in transport pathways is somehow responsible for variability and not for systematic variation.

2./5. Your discussion of the relevance of your results to the millennium drop needs to be further clarified.

3./6. have been dealt with to some extent.

4. I think that there has been some clarification here, but there could be further improvement.

Having looked at the paper myself, and taking into account Referee 2’s comments, I see the paper as now in a state of potentially publishable if revised further.

I have set out a list of detailed comments below. Please consider these in addition to those from Referee 2 and provide a revised version of the manuscript, plus responses as appropriate that address my comments and those of Referee 2.

I hope to accept the paper after further revision and without further consultation with referees.

DETAILED COMMENTS:

p1 l20: ‘these regions’ > ‘these two regions’/‘the polar and the tropical regions’

p1 l21: ‘During an EN event’ — of course all this is subject to internal dynamical variability — see for example Hardiman et al 2008.

p2 l19: ‘moreso’ > ‘more’?

p2 ‘led to 0.14ppmv of dehydration, explaining approximately 23% of the observed drop in water vapor over this period. ‘explaining approximately 23% of the observed drop’ seems a slightly absurd statement. (There is a similar statement in the abstract.) Surely ’around one-quarter’ would be a much better way of saying this. Also at some point in the paper you need to say carefully what you mean by this — you are deducing from a large ensemble of AGCM simulations with imposed SSTs that the deterministic part of water-vapour drop arising from these imposed SSTs is about one-quarter of that actually observed.

p2 l33: ‘such that ENSO variability aliased onto sub-decadal variability’ — I suppose that if one thinks of analysis of interannual variability as a kind of black-box exercise in time-series analysis then this comment makes some kind of sense. But my suggestion is omit it.

p3 l4: It seems to me that in the end you are seriously questioning the use of linear regression only with respect to water vapour (and you don’t really have any grounds for questioning its use beyond that). You need to make that clear.

p3 l19: ‘The source of this nonlinearity is the Indian Ocean response to EN’ — this is a pretty strong statement — you are providing some evidence for this. Make it clear that this is a suggestion, not a fact.

Figure 1: This is labelled ‘relation between Indian Ocean and ENSO near surface temperatures’ but the field being considered is 50E-150E temperature, which you refer to you yourself as ‘Indo-Pacific’. Only about half the 50E-150E region is the Indian Ocean. Clarify this.

p3 l24: ‘The tendency of EN events to lead to a warmer Indian Ocean is well captured by the model.’ As noted in previous comment this can’t be deduced from what is shown given that only about half of 50E-150E is Indian Ocean. Amend.

p5 l15: ‘Model output necessary to run a Lagrangian trajectory model for these simulations was not archived and hence we cannot quantify the specific location of dehydration.’ Something like this comment was requested by Referee 1 and is needed somewhere but it seems out of place here. It is really an analysis/interpretation issue rather than a model issue. The important general point is surely something like ‘Full explanation of inter annual variability in stratospheric water vapour, particularly that associated with El Nino (Bonazzola and Haynes 2004, Hasebe and Noguchi 2016, Konopka et al 2016), requires consideration of both a ‘sampling effect’ and a ‘temperature effect’. These two effects cannot be distinguished in our simulations, since the model output necessary to run a Lagrangian trajectory model was not archived. Nonetheless neither is prevented from operating in the simulations and the simulated interannual variability in water vapour will arise from some combination of the two.’ — that needs to be said somewhere in the early part of the paper and I suggest (given that Referee 1 raised this as an important point) that it is also repeated somewhere in the conclusions.

p5 l30: ‘ENSO events in the simulations’?

p6 l10-13: I found these sentences very difficult to understand. For example by ‘moistening of the stratosphere during El Nino is more pronounced that expected’ you mean something like ‘the El Nino moistening signal is stronger if the BDC is not regressed out of the water vapour signal’ but I can’t tell exactly what. Terms like ‘more pronounced than expected’ often cause problems because it might be what you expect but it might not be what someone else expects.

p6 l17-21: This paragraph is also not easy to understand. ‘many of the complications that arise due to the QBO (e.g. Liang el al 2011) are not relevant’ is I believe your particular take on the fact that there is a strong QBO effect on e.g. tracer distributions in this region — which are the subject of the Liang et al paper — but that in your ensemble of simulations there is no time coherence of the QBO across the ensemble — so when you consider any kind of ensemble average then you do not expect to see any coherent QBO signal. However you do apparently take account of the QBO when you compare against observations — though I don’t understand exactly what you mean. Do you mean that the QBO signal is taken out of the observations? or out of the simulation results? This is further confusing because you seem to have ‘removed’ the QBO in Figure 2 and ‘detrended QBO regressed’, whatever that means in Figure 3 — but neither of those individual Figures seems to involve ‘comparison against observations’. Clarification is definitely needed.

p6 l24: ‘on Figures of temperature at 100hPa’ — telling the reader exactly which figures would be helpful.

p7 l3: ‘from the late fall through late spring’ — both of these are NH of course (as are presumably any references to season).

Figure 2: The markers are very small. I found it almost impossible to distinguish between blue and black, for example. Please modify. The letters and numbers in the Figure annotations/extra information are also very difficult to read. Sometimes these numbers, e.g. R^2 values, are important. Please modify.

Figure 3: Are (d),(e),(f) correctly labelled — currently as ‘Mar-Jun’? You might note explicitly somewhere the very large role of internal variability as manifested by the very large spread in values across the ensemble. Actually there is presumably no particular difference in this between the AGCM simulations and the coupled simulations — it is just that with the coupled simulations the number of ensemble members is much smaller so pattern of spread in values is less ‘full’.

Figure 3 caption: ‘integration’ is presumably the same as ‘ensemble member’.

p7 l16: ‘Even if we linearly regress out the BDC the slope … (not shown).’ Given that the results can’t be seen is it really important to make this point here?

p8 l2: Is it really fair to describe Figure 4 as ‘the observational constraints’ or indeed to put any significance that the simulations fall within such ‘constraints’ (in a sense that you haven’t precisely defined). From my point of view the single 30-year or so time series of the observations might be expected to fall within the envelope mapped out by a large ensemble or such time series, not necessarily the other way round. As you seem to say, the ‘nonlinearity’ in Figure 4 seems to come down to the presence of the year 1997/98 — the extra information added by the nonlinear curve fitting — with a small value of R^2 — is not at all clear.

Figure 5: I’m assuming that in this figure some effect of the QBO signal has been ‘taken out’ (whatever that means exactly). It might actually be most useful to postpone proper explanation of this until this point and then explain it clearly.

p8 l11: ’0.4 ppmv in late (NH) spring’ — the value of 0.4 ppmv looks to me to start only in June — isn’t that NH summer, not NH spring.

p8 l12-23: This discussion in the difference in the shape and location of cold point regions in 97/98 versus other years is quite difficult to follow and I’m not sure that your addition of particular coloured temperature contours has succeeded in making things clear. But if you cannot see a better way to do things then so be it.

p8 l30: ‘this nonlinearity in the temperature and water vapour response appears to originate from the troposphere’ — isn’t the most compelling reasoning for this simply that in the AGCM simulations (which you are considering) the ‘input’ signal is the SST field. But what do you mean by ‘originate from the troposphere’ exactly? Do you mean ‘does not involve stratospheric dynamics’?

p9 l13: I’ve already noted in a previous comment then if you are particularly emphasising the role of the Indian Ocean then using an index based on the ‘Indo-Pacific region’ 50E-150E, half of which is not in the Indian Ocean, seems not the best choice.

p9 l17: You show curves regressing out the BDC and linear regressing out the QBO. So do I conclude that the QBO signal is retained in the curve which regresses out the BDC. Why? The importance of these regression coefficients depends of course in part on the magnitude of the temperature variations in the different regions. The coefficient for a particular region could be large but the magnitude of the temperature variation could be small. You should comment on that.

p9 l23: ‘In the annual average, warmer near-surface temperatures over the Central and Eastern Pacific lead to dehydration of the stratosphere in all three data sources’ — for clarity, what features exactly in Figure 9 are you identifying that prompt you to say this?

Section 6: Referee 1 asked for more clarity on what you mean by the millennium drop and you have made some modifications, but there still seems to be scope for further clarity. I suggest that you move and modify your sentence p10 l23-25 to close to the beginning of the section. Then it is clear to the reader what you mean by the drop and also what aspects of the drop — e.g. the detailed time evolution of the late 2000 and early 2001 period.

p10 l31: ‘Hence SST changes contributed to the drop … but were not the major forcing factor …’ — these seem to be overconfident conclusions. You need to say something more measured — e.g. ‘on the basis of your large ensemble of AGCM simulations, the imposed SST signal can account for a ensemble average water vapour drop (by your definition) of about 0.14pmmv. This suggests that … ‘.

p10 l32: ‘consistent with Garfinkel et al (2013b)’ — actually in this paper you say nothing at all about ‘the drop’ as far as I can tell. So I don’t understand why you are referencing it. In the reference list you also have the title (of your own paper!) listed incorrectly — it doesn’t match the title of the paper that appeared. For that matter Garfinkel et al (2013) is presumably no longer ‘in press’.

p10 l32-33: ‘The magnitude of the drop is 0.09ppmv if we consider water vapour area weighted form 60S to 60N.’ I don’t understand why this sentence has been included. It doesn’t seem to reference anything else. Omit?

p11 Figure 11bc: To me these figures on cloud ice is a distraction. No detailed discussion is given. This is the first time that cloud ice has been mentioned at all in the paper. Figure 11c shows December and increased cloud ice over the Central Pacific when in the rest of the paper you seem to have been emphasising that moistening occurs in ‘NH spring’ and is more associated with processes over the Indo-Pacific region etc. There seem to be increases of up to 2ppmv at 85hPa which doesn’t fit with the statement of ‘even at 85hPa cloud ice increases by 0.05ppmv’. I recommend to postpone any discussion of cloud ice to a further publication where details can be presented properly.

p11 ll16-17: ‘Hence in summary, strong EN events lead …’ — OK, but it is slightly confusing the previous sentence is completely unrelated to this.

p12 l4-8: Again this conclusion confuses ‘truth’ with a useful line of argument deduced from an important set of model simulations. We don’t actually know if the ‘enhanced’ water vapour in 1998-2000 was due to El Nino/La Nina or not. What we do know from your simulations is that providing observed SSTs can lead (in the sense that it leads to an ensemble average signal) decrease in water vapour from 1998-2000 to 2002-2004 of 0.14ppmv, so it that sense some of the observed drop may well have been ‘caused’ directly by the SSTs. You say that this accounts for ‘approximately 23%’ of the observed drop. I might say this shows that ONLY about one quarter of the drop can be directly accounted for by the SSTs.

p12 l21: ‘However these sampling effects are included implicitly in GEOSCCM’ — that is fair comment. (See other comments above.) ‘some of the diversity in response among the 42 ensemble members to an identical SST forcing is almost certainly due to such sampling effects’ — I don’t understand why this statement is being made and it might be revealing a confusion. Ensemble members with the same SST forcing will differ in both TTL circulation and TTL temperature and in that sense both ‘sampling effects’ and ‘temperature effects’ will lead to differences between such ensemble members. There is no sense in which ‘sampling effects’ are more about inter-ensemble variability and ‘temperature effects’ are more about ensemble mean response. The ensemble mean response includes both temperature effects and sampling effects. The inter-ensemble variability includes both temperature effects and sampling effects. Again it seems to me that you simply need to be candid and say that the effects you are identifying are likely to have a contribution from temperature effects and a contribution from sampling effects and in the absence of further information you can’t distinguish between the two and can’t say anything more.

p12 l23: You keep referring to ‘the Indian Ocean’ but you also refer to ‘Indo-Pacific’ and many of the measures that you use include longitude that are not in the Indian Ocean. It would be helpful if you could be as clear as possible on these points.

The paper is very close to being suitable for publication. I still have the view that you have not been sufficiently clear about the definition of post-2000 drop and what aspect of that you can address. I have previously noted that this was a significant concern of Referee 1 and I don't feel that this has yet been addressed satisfactorily.

Please address the comments below in a further revision of the paper and either make changes or provide good reasons why changes are not needed. It is the 'drop' that is my main concern -- other points are relatively minor.

Definition of millenium/millenial/post-2000 drop:

Referee 1 asked for clarity on this. Your reply re Section 6 says that you have provided this but there is still plenty of scope for improvement. At the end of the first paragraph of Section 6 you have said ‘the experiments can be used to quantify the contribution of SSTs to the difference in water vapour between 2002-2004 and 1998-2000 and with these caveats duly noted we now proceed.’ That’s fine — you have clearly defined a drop whose causes can be assessed by your model simulations. But in the abstract you still have ‘drop in water vapour in late 2000. … This … [SST] … effect accounts for approximately one-quarter of the observed drop’ — which claims that you can account for a change on much shorter timescale than 2002-2004 vs 1998-2000. Please correct that particular point and re-examine your use of ‘drop’ across the whole paper.


p1 l10: ‘millennial’ — you have used ‘millennial’ in most places but ‘millennium’ in at least one place. You have used ‘post-2000’ in the title to Section 6. I suggest you use a single term.

p5 l3: You refer to Indo-Pacific warm pool here but actually Figure 1 also shows the Indian Ocean (50E-100E) temperatures which doesn’t mentioned until a few lines later. Why not say straightforwardly that Figure 1 shows both Indian Ocean and Indo-Pacific warm pool. Also the fact that both ‘Indian Ocean’ and ‘Indo-Pacific’ are shown is not clearly stated in the caption nor in the annotation to Figure 1.

p8 l25: You use ’nodal line’ then ‘zero line’, then you refer to contours — things could be clearer.

p8 l33: ‘The eastward shift in Figure 6b and 7ab is consistent with the shift in the Lagrangian cold point evident in figure 8 of Hasebe and Noguchi (2016).’ — good that you are referencing previous work. I can’t resist commenting (without implying that any action is needed) that the same shift — again for the 1997/98 El Nino — is shown in Figures 8 and 9 of Bonazzola and Haynes (2004).

p10 l20: ’Strong EN events tend to have a stronger impact on the Indian Ocean than more moderate events (cf Figure 1).’ — this is true in the sense that there is a positive and essentially linear correlation between an EN measure and Indian Ocean temperatures, but no more than that (e.g. no nonlinearity is evident).

After your further minor revision I am pleased to accept this paper for publication in ACP.