Review of “Observed impacts of aerosol concentration on maritime tropical convection within constrained environments using airborne radiometer, radar, lidar, and dropsondes” by Amiot et al.

Recommendation: accept after revisions

Overall evaluation: This paper investigates links between various observed atmospheric parameters and the moist convection strength with the overall goal to understand aspects of the so-called convection invigoration. In other words, the motivation is to explore links between factors that in theory can affect moist convection and observed convection strength. The observations come from the CAMP2Ex experiment.

First, I have to say that I am not the right person to review this submission. Although I was involved over the last decade in the discussions of the invigoration conundrum (and for that reason I am signing my review), I feel someone with more expertise in atmospheric observations should also be involved. In particular, I feel the observations lack estimates of their uncertainty. Since this is not my area, I am not sure what to suggest. One possible suggestion is to use a spread of the observations near (in space and time) of the convective event. But this aspect can only address the sampling problem, that is, an uncertainty of a single observation. Another important aspect is an accuracy of the observation itself or uncertainty of a retrieval algorithm. I am not capable to assess if that aspect is appropriately addressed in the submission.

Below I discussed two major points concerning this submission, and follow with several specific comments that require authors’ attention.

Specific major comments.

I have two main issues concerning the motivation and interpretation of results. For the motivation, the convective invigoration discussed in the introduction is poorly explained. There are important published studies that discuss and criticize the original convective invigoration proposal of Andreae et al. (2004) and Resenfeld et al. (2008), including my own papers, that should be included in the introduction. The recent review paper by Varble et al. (ACP 2023, https://doi.org/10.5194/acp-23-13791-2023) should definitely be cited for that.

For the interpretation, I strongly object the suggestion in the summary section 5 that the results support the notion of enhanced aerosol concentrations may invigorate convection (e.g., lines 501 and 510). The key problem is that the correlation does not imply causality. Is it possible that higher aerosol concentrations simply occur in conditions supporting stronger convection (e.g., higher CAPE)? The text in lines 512-515 seems to suggest that such a conclusion might be valid. One suggestion would be to explain the correlation versus causality conundrum in the introduction, and then try to use the results to shed some light on the problem.

However, I have to admit that the discussion of the results in sections 3 and 4 are difficult for me to follow. Specifically, I do not see any trends in figs. 3, 6 and 9, just scattered data points. Does that suggest that the overall outcome of the study is inconclusive? Is there a better way to present the results? See 7 below.

Specific comments.

1. The paragraph starting in l. 68 and the reference to Mulholland et al (2021) in particular. The argument here is wrong as discussed in Grabowski (QJRMS 2023), see the summary Fig. 17 there in particular. Please revise keeping in mind that the argument in my paper applies to convective boundary layer over land. Such an argument might not always apply to oceanic convection with weak surface buoyancy forcing. The above comment is also relevant to the discussion around l. 156. Specifically, it is unclear to me why higher LCL may favor stronger convection.
2. L. 156: It is unclear what you mean by “frequency” here and in other places (e.g., l. 214). Do you mean higher cloud cover? Please explain or remove to focus on the convective intensity alone.
3. L. 109 and later in the text. I was confused by units of CLW and I though it should be kg m^-3 (i.e., content). That was until I realized that this is the CLW path. I suggest to use CLWP throughout the manuscript to avoid confusion.
4. The discussion in paragraph starting in l. 119. Please see me major comment above. Perhaps referring here to postulated “warm” and “cold” invigorations would be appropriate here. However, see the discussion in section 2 in Grabowski and Morrison (JAS 2020, p. 2567) and the review of Varble et al. (2023) already mentioned above.
5. L. 186 versus l. 63. Overall, CAPE refers to the buoyancy integral from the level of free convection to the equilibrium level as given by (1). Integrating buoyancy to the aircraft altitude as in (4) gives only a fraction of CAPE as pointed out in the submission. I feel the authors may want to refer to what I call “cumulative CAPE” (cCAPE), that is, how CAPE builds up in an adiabatic parcel as the parcel rises through the atmosphere. I feel this is a useful concept as shown, for instance, in Thomas et al. (ACP 2018, Fig. 4 in particular) and in some of my papers concerning convective dynamics (e.g., Grabowski and Morrison, ACP 2021, see Fig. 3 there). Clearly cCAPE depends on the aircraft altitude, so it is unclear how important that aspect is for the analysis. Can some large-scale analysis be used to extend calculations above the aircraft altitude to get the total CAPE?
6. Table 1 should include units for all symbols.
7. Figs. 5. 7, and 8. These are not figures, these are tables. It is difficult for me to draw any conclusions looking at them. Can they be shown as bar diagrams? I think the authors need to think about a better way to show those key results.

Signed: W. Grabowski.