One referee now recommends that your paper is suitable for publication after further minor revision. The other referee has written what seems to me a very helpful report confirming that in your revision you have satisfactorily addressed one important aspect of his/her original criticism but arguing that the second aspect of his/her criticism regarding calculation of radiative damping rates has not been satisfactorily addressed.

My view is that this referee makes an important point. Therefore please can you provide a revised of the paper that addresses the referee's concerns and also the various more minor comments that are made by both referees.

I have categorised what is required as major revision because I see it as quite important -- however my hope will be that your response on this will be sufficiently clear that I will feel able to accept the paper without going back to the referee.

To quote the relevant part of the referee's report:

"In light of these concerns, the substance of my recommendation for major revisions from my previous review still stands: The usage of the Plass value of 50% [or 30% in V2] should be either (1) justified in light of these considerations or (2) an alternative reliable estimate should be provided of the radiative damping rate response to CO2 doubling (an order of magnitude estimate is fine). If no projection of radiative damping rate with CO2 doubling exists in the literature, then one should be produced (e.g. using a radiative transfer model). Such a projection of radiative damping rate, necessary for the arguments in the paper, would constitute a valuable contribution in its own right."

You will see that there are various ways of addressing this -- the important point is that the current quoting of the Plass results to motivate an estimate of change in damping rates seems to be unsatisfactory.

Incidentally, in looking through your paper again I noticed the comment -- 'Fels
(1985) explicated why this cooling rate is suitable for simulating the QBO on the basis of the scale-dependent effect of radiative damping (Fels 1982).' -- 'explicated' should be 'explained' but the way. But it seems to me that Fels (1985) didn't actually make a statement that was a clear as what might be inferred by your sentence. One example of what Fels actually says is
"For internal waves, and many of their equatorial cousins, however, an accurate representation of tau_r is important; for such disturbances, radiative damping can be the dominant dissipative process, and their wavelengths are such that the local approximation is very poor." -- by 'local approximation' Fels means that heating/cooling rates depend only on local temperatures and therefore the damping rate is not-scale dependent. I am not suggesting that you need to change your representation of radiative damping in any substantial way, but I think that you could be a bit more cautious on how you justify it.

My final thoughts concern the abstract. Since in the 1-D model the only effect of radiation is on the (parametrised) waves, whereas in 3-D reality changes in radiation will affect upwelling, secondary circulation, tropical wave sources, etc, etc, (some of which you mention) it would be helpful if you made it clearer that it is the effect of the radiative damping on the waves that is being investigated. Additionally what is meant by the first two sentences is not clear -- you say 'we find that when atmospheric carbon dioxide increases' -- but that might give the reader the impression that you have actually implemented a change in carbon dioxide in some way. In fact what you have done is change the damping rate (in a way that you justify as a possible effect of increasing carbon dioxide -- and it is of course quantitative justification that continues to concern the referee).

You have made substantial changes in response to the comments of the two referees, so the paper is now closer to being suitable for publication. However having looked at the revised paper carefully my view is that way in which the changes have been made is potentially confusing. I was considering sending the paper back to the referees for their comments, but have decided against that for the moment.

I have set out below the two aspects of the revision that I see as confusing. Please consider making appropriate changes or else provide responses arguing why no change is needed.

I hope to be able to accept the paper for publication at the next stage of the process, but to do so I need to feel that the referees' comments have been properly addressed, in a way that does not confuse the reader.

(1) radiative damping

Referee 1 made the point that the Plass (1956) paper which you originally used to motivate and quantify increased damping rates associated with increased CO2 really says very little about change in damping rate. As the referee recommended -- and I think this is the approach you have taken. But you still make significant reference to Plass (1956) as you present the details of your approach.

The bottom line is that the idea of damping rate and ways to calculate is well-developed in the literature, including the idea that damping rate may change as a result of increased CO2 -- see Fels (1985) for example. Bringing in Plass (1956) and then explaining why his results are nor relevant is a complete distraction. If you want to acknowledge to the contribution of Plass (1956) in, for example, recognising that the radiative properties of the stratosphere will change with increased CO2 then do that in the introduction -- though his was one of several contributions on effects of increasing CO2, with the paper of Manabe and Wetherald (1967) being the most frequently cited (appropriate in my view if one takes account various important innovations in their calculation).

I have given 3 examples below where the text needs attention in this respect.

l128-133: "Given the fact that the QBO period is influenced by the radiative damping (Plumb 1977; Hamilton
1981), a natural question to ask is whether it could play a role on the trend of the QBO in a warming
climate. Plass (1956) showed that when the CO2 concentration is increased from 330 ppmv to 660 ppmv,
the cooling rate increases significantly in the middle and upper stratosphere while it is not changed below
the 24 km height level. The cooling rate is increased by about 50% around the 40 km height level (see
his Figure 8)."

If we agree that Plass's calculation tells us little about damping rate -- then the above sentences are very confusing -- most reader will assume that there is a connection between 'radiative damping' in the first sentence and 'cooling rate' in the second.

l207-216: "Since the cooling rate is increased by about
50% around the 40 km height level (Plass, 1956), the radiative damping rates are expected to also
increase in the middle and upper stratosphere as the CO2 concentration rises. However, the relative
change of cooling rate 𝑄 in response to the increasing CO2 is not identical to that of Newtonian cooling ..."

Again the Plass has very little useful relation to the proper calculation of damping rate, so what is the point in referring to Plass (1956) and then saying in the following sentence that a different calculation to that in Plass (1956) is needed ...?


l222-226: "In FIG. 1b the black line depicts the ratio for the broadband longwave radiation (5 𝜇𝑚 −
9#(-;<) + 9#(-)
100 𝜇𝑚) and the red line delineates the ratio for the CO2 absorption band (12 𝜇𝑚 − 18 𝜇𝑚) used by
Plass (1956). For the CO2 absorption band, the calculated ratio is evidently comparable to the ratio of
cooling rates between the doubled CO2 and the reference CO2 shown in figure 8 of Plass (1956), with an
additional small increase (<1.1) below the 24 km level."

Again, what is shown in your Figure has very little to do with Plass (1956) -- his Figure 6 shows cooling rate -- calculated on the basis of a fixed temperature profile and various CO2 concentrations. An essential part of your calculation is the heating/cooling rate difference arising from a temperature difference. In trying to bring in Plass (1956) here you are actually undermining the credibility of your own (updated) calculation.

(2) Effect of ozone

Referee 2 suggested that the effect of changing ozone on the QBO might well be as important as that of changing damping rates due to increasing CO2.

You don't mention the possibility of an ozone effect on the QBO until Section 4. (You mention the effect of the QBO ozone earlier, but that is different.)
Then suddenly you give l344-354, which focuses only on the effect of ozone on the thermal damping rate, via its long-wave effect -- and essentially dismisses any role for ozone, when your reply to the referee has seemed to say that ozone is complicated and the resolving the role of ozone is not within the scope of your paper.

In order for the reader not to be confused by this there needs to be some introductory sentence somewhere which introduces the idea that changes in ozone may be important and furthermore it needs to be acknowledge that changing ozone may affect the QBO in other ways -- for example the Hasebe (1994) paper focuses on the short-wave heating role of ozone. As with your paper as a whole, you are in any case considering only one part the QBO mechanism -- the radiative damping of planetary-scale waves -- when there are many other parts of the QBO mechanism that may change as a result of increasing greenhouse gases -- and that includes parts that involve changes in ozone. You acknowledge this point in a fairly general way in the final sentence of your abstract and more clearly in the final sentence of the paper. Your paper will be more, not less, valuable if you make this point as clear as possible.

You have addressed the two concerns that I expressed about the previous version of the paper. (You have provided a more detailed discussion of ozone effects than I was expecting, but that is OK -- my concern on lack of clarity re the range of possible ozone effects has been addressed.) Therefore I am pleased to accept the paper for publication in ACP.