Dear Authors,
I have weighed the reviewers' comments, re-read the revised manuscript, and reached the conclusion that I cannot accept the manuscript until major changes are made, including changes in organization, analyses recommended by the authors, and careful choice in how conclusions are stated. The reviewers uniformly have significant points and two have problems with the quality of the science.
I list key issues, my own comments, and some editorial comments below.
Please consider all points carefully and revise the manuscript accordingly. I would like a revised version to meet the reviewers' standards so I can reach a positive decision, but there is still much to be done.

Graham

A sample of important issues raised by the reviewers that must be addressed. (I'm not implying that others don't need to be addressed.):

1) The paper should lead with the observations. The models have indirect effects ‘baked in’ even at the ’convection permitting’ resolution so the hypothesis posed at the top of pg 12 rings a little hollow.
Please more clearly delineate observations and modeling, as requested by the reviewers.

2) The regression analysis presents problems. First, one cannot draw conclusions about causality because of co-variability. Granted, the wording around the regression analysis doesn’t suggest causality but the closing statements in the abstract and conclusions do. Second, it is very difficult to judge whether the regression fit of the proposed power law is good enough for quantitative conclusions to be drawn (only ~ 65% of variance in CLWP is captured). Fig. 11 is not helpful. Please carefully reconsider how you present the regression analysis.

3) The elimination of the Holhuraun volcano study, which is inconvenient for the main (relatively strong) conclusions, presents a problem, as noted by Reviewer 1. In the current version that study is only peripherally referred to. The fact that the re-working of that analysis suggests weaker evidence for aerosol-cloud interactions might require separate publication, but now that you are in possession of that knowledge it cannot simply be brushed aside. You would do better to discuss it.

4) Regarding the modeling, Please provide more clarity on key components of the microphysics. The dependence of Nd on aerosol and updraft is discussed at length but what autoconversion scheme is used? This is probably a more important issue than activation. Some autoconversion schemes have particularly strong dependence on drop concentration while others do not and this has significant impact on aerosol-cloud interactions.

5) Many of the supplementary figures indeed belong in the main text. Please reconsider the distribution.


Some specific comments of my own:

1) In the opening lines of the abstract there is a conflation of 21st century climate change and aerosol effects on midlatitude cyclones. Climate change does not equate to increases in N_d (drop concentration).

2) Pg 5, lines 1 and 14: N_d is not retrieved at cloud top. It is based on cloud top effective radius and (path integrated) cloud optical depth

3) Pg 6: perhaps cloud property retrievals are not subject to thresholding but you still have to define cloud fraction so that all sky albedo can be calculated. How is cloud fraction defined? Is it consistent amongst analysis and model output?

4) Pg 7, “microphysics and aerosol explicitly interact” is a bit strong. The statement is true but a bit misleading given the resolution.

5) Pg 9, line 6: “disentangling”. It seems like the meteorology is fixed and the aerosol is changed but this isn’t what happens in nature so are you really disentangling anything of value? (see e.g., Feingold et al., PNAS 2016).

6) Pg. 10, line 15, what does “lifetime effect” mean in the context of a midlatitude cyclone. This terminology is vague at best. (See editorial comment below.)

7) Pg. 10, Fig. 2: how many simulations were performed. The observations average many initial conditions and aerosol-meteorology co-variability. Do the models all use the same initial conditions?

8) Since aerosol concentration is fixed in the modeling, aren’t you biasing your aerosol effects to be much stronger than would be the case if aerosol were washed out by the rain? If CASIM is indeed two-moment, it should remove aerosol and allow N_d to fluctuate accordingly.

9) Pg. 14, lines 8-15: Wouldn’t the open cells be raining and have low N and lower domain-averaged liquid water path?



Some editorial comments:

1) What do you mean by cloud-aerosol lifetime effect? This concept is particularly poorly defined. It doesn’t reflect on the lifetime of the midlatitude cyclone. I assume you mean a reduction in precipitation efficiency. Regardless, please be precise.

2) Acronyms like CDNC, while widely used, are bad practice since they can much more easily be represented by symbols (N, perhaps with subscript d) as you already do for aerosol concentration. The excessive use of acronyms will make papers in our field unreadable if we are not more careful. CLWP could be replace by L_c, SZA by \theta, CF by f_c, etc.
While I don’t insist on these changes, please consider that they really help with clarity, particularly for those entering the field. (See pg. 15, what is CDNCSW??)

3) CCN, again is widely used, but has no quantitative meaning unless defined at a specific supersaturation. You might as well use the same symbol as for accumulation mode aerosol number concentration if indeed they are used interchangeably.

4) The manuscript has some lapses in grammar (e.g., Pg 3 lines 20-22)and could benefit from some liberal use of commas in some places.

5) Many figures and their fonts are much too small to be readable in print form.

Dear Authors,
I have read your revised document and find it improved. I am willing to tentatively accept it for publication without a third round of reviews, provided attention is given to a number of remaining issues. Please pay careful attention to these so I can make a final recommendation for publication.

Graham

Abstract:

“When CDNC is increased in the simulations, the CLWP consistent with a given WCB moisture flux increases.” This is a key point of this paper but the wording here is not clear, especially since this is the first time it is introduced. I urge you to reword it along the lines used in the conclusion: “When CDNC is increased a larger LWP is needed to give the same rain rate. The LWP adjusts to allow the rain rate to be equal to the moisture flux into the cyclone along the warm conveyor belt.”


Pg 4: “Cyclone centers” (not Cyclones centers)

Pg 5: “crosstalk” is technical. Please avoid this terminology and just state what the issue is.

Pg 6: The power law form of the relationship between Nd and sulfate is clearer.

Pg 10: The discussion of fixed Nd is unnecessarily complicated and needs some work. Please state more suscinctly that you are assuming replenishment = removal and discuss implications (e.g. what are the conditions under which it is more likely to be true. You could back this up with some simple calculations along the lines of Wood (doi:10.1029/2012JD018305).

Pg 11: The discussion of “dynamical feedback” is out of place. First it’s not even defined, leaving the reader to wonder what you are referring to. Second, one cannot expect coarse resolution simulations that use saturation adjustment to represent these effects. Please streamline this discussion and remove unnecessary references.

Pg 12: “as it should be a consequence of mass conservation”. This is a statement that could be contracted to clarify the point.
Why not: “This consistency across models of varying spatial resolution and observations of real-world cyclones seems reasonable because once in equilibrium, the water mass flux that goes into the cyclone must be precipitated out.” (or similar)

Pg 17 and 18 (and other instances): MODIS does not “observe” Nd; rather MODIS measurements of tau and r_e are used to “retrieve” Nd.

Pg 19: I’m still not convinced that CASIM doesn’t “bake in” positive LWP responses to Nd at the grid spacings employed in this model. I do agree that CASIM should be able to represent other responses at higher resolution. See, e.g., recent NICAM results by Y. Satoh et al.

Pg 21: 3.4 “Differences in the structure of clouds within cyclones as a function of Nd”

Pg 26 (top) “position… is reversed” or “positions… are reversed”
Pg 26: “as would a cloudy sky albedo”

Pg 28 (and elsewhere) I think you could be more quantitative than “majority”. Why not “up to two thirds”?

Pg 30: “anomalous at the 95% confidence level” (and anomalous in what regard?
Pg 30: “While evocative…” evocative in what regard? Increasing LWP? Please be clear.

Pg 31, line 3: If you mean that “no longer being different at the 95% confidence level” means “no aerosol effect on LWP” then please be clear.

Pg 31: “Overall, we find agreement with the results presented in Malavelle et al. (2017) in that models [that] strongly adjust LWP in response to this eruption are likely to over-predict aerosol-cloud adjustments.”
This sentence states the obvious.

Pg 32 and abstract. I think this is the key message of this paper (at higher aerosol a larger LWP is required to allow the rain rate to equal the moisture flux) and that you can do a better job conveying this.

Pg 33: There are still quite a few grammatical lapses that one might hope the technical editors will pick up, but in lieu of that, a careful read would be helpful. Language can definitely be tightened in various places.

Dear Authors,
I have reviewed your manuscript and am happy to accept it for publication in ACP.
Best,
Graham