|Review of the revised manuscript “Impacts of Cloud Microphysics Parameterizations on Simulated Aerosol-Cloud Interactions for Deep Convective Clouds over Houston” by Zhang, Fan, Li, and Rosenfeld, considered for publication in ACP, manuscript acp-2020-372.|
Recommendation: additional revisions needed
The revised manuscript has been improved. In particular, the invigoration (that is really only tangentially related to this study) is now better presented as still a controversial subject requiring additional studies. First, let me note that not all of my points have been addressed. In particular, I suggested that the two schemes applied in the simulations, and specifically their ice components, need to be explained in more detail (see my previous point 7). The additional material added in the revision provides some confusion to me, see below. I would either expand the analysis or remove part of that material to create no confusion, see specific comments below. This material is really not needed for the main thrust of the paper, and it should be suitable for a future manuscript when more analysis is done. Perhaps the most significant comment at this stage is that in my opinion the authors provide a bias interpretation of some of the figures. I present specific examples below. Also, some figures require adjustments as detailed below.
I should also mention in passing, that I am not fully satisfied with our previous exchanges, the quasi-equilibrium supersaturation discussion in particular. However, since this aspect is not part of the manuscript, I will put this issue aside, perhaps with the exception of the comment 2 below.
1. The first sentence of section 2 is a repetition of the text a couple lines above, at the end of section 1. Please remove either one.
2. L. 228-229: What do you mean: “…the supersaturation for condensation and evaporation are calculated after the advection”? Do I understand that the model advects temperature and water vapor, and then combined the two to create supersaturation that is subsequently applied in microphysical calculations? If so, this is simply wrong as supersaturation calculated this way has no physical meaning and it depends on the time step applied in the advection (the longer the time step the larger the supersaturation calculated this way). If this is how WRF model works, this is a shame. There are different methods to do this correctly. See, for instance, the seminal paper by Hall (JAS 1980, p. 2486; see discussion in section 3e). My suggestion is to remove this sentence and not to open the Pandora box. But this is something to think about for the future.
3. Figure 3: as in my previous comments, there are more points with different colors than in agreement with the model. The phrase “though not exactly the same” in l. 258 in a stretch. My suggestion is to remove this figure and only include Fig. 4, maybe with the time averages. But if the goal is to show the spatial pattern, then please say that the model represents the spatial pattern, but has problems with specific measurement sites, not surprisingly I would think.
4. Figure 4. The comparison between model and satellite estimates is difficult. Maybe scatterplots (i.e., one versus the other, without geographic information) would be better?
5. Figure 6. Models are close to each other and they both miss to represent E-W temperature gradient apparent in the observations. Why?
6. Figure 7 is really nice, but its discussion in the text is not. First, it is great to see that all model realizations feature a cluster of convective cells in the red box (as in observations), and some convection NE to the red box. Is the position of the cluster inside the red box related to the aerosol gradient between the Houston and its vicinity? I am also not sure if I see the differences the text emphasizes. To me, model results are simply slightly different realizations of the same convective situations. If anything, the SBM realizations look a little more “diffused” to me.
7. Figure 9 and its discussion. First, I prefer to consider rain accumulation, not intensity, as more instructive. The upper panel has to include line definitions. Models start earlier than observations, solid lines before dashed (I do not know which one is which). To me, all lines are simply different realizations. Bottom panel: the anth and noanth reverses in both schemes between small rates (noanth larger) and high rates (anth larger). This should be mentioned. I suggest to use linear scale (different for different rate ranges) as the linear scale shows much better the difference. The way the figure is plotted now (rate rather than accumulation in the upper panel and log scale in the lower panel) is suboptimal. The text emphasizes differences (“remarkable” in l. 321) that I do not see. The same for the difference between SBM and MOR: the lower panel shows similar trend and I do not see what the text says in lines 321-325.
8. Figure 10. The impact of pollution is remarkably similar in both models. I do not see much invigoration below freezing levels (that may come from different supersaturation treatment in SBM and MOR) and there is some aloft. But where it does come from for MOR? Maybe because of difference in ice processes? But we do not know how ice processes differ in the two models. This comment is also important to understand the impact of supersaturation prediction in MOR simulations.
9. Figure11. Left and right panels (SBM and MOR) are remarkably similar. NB, I commented before that the term “thermal buoyancy” has to be replaced by “buoyancy”; “thermal” is confusing because buoyancy has to include temperature and all water variables. The difference between MOR_noanth and MOR_anth has to do with different flow realizations, at least below the freezing level (again, what about ice representation?). There is no other explanation unless one argues about the feedback from rain processes. The MOR_SS results are unexpected as it shows the opposite impact of including finite supersaturation on the mean updraft, buoyancy, and latent heating. The rest of the manuscript tries to explain this surprising result.
10. To understand the effects of supersaturation prediction in MOR_SS simulations, one needs to know more details on how the prediction is linked to the microphysics. For instance, how does the change affect the droplet activation and ice processes? Grabowski and Morrison (JAS 2017, p. 2247) document some impacts on ice processes when saturation adjustment is replaced with saturation prediction. Do you still use Ghan et al. droplet activation parameterization when predicting supersaturation? How ice initiation is affected? Fig. 13 shows that saturation prediction has small impact on droplet activation (mass-wise), but large and unexpected impact on the condensation rate. How is the latter possible? I think an attempt is made to explain this in the rest of the paper, but I suggest to remove that part and MOR_SS simulations altogether as only tangentially related to main results of this study.
11. Figure 13: what is “condensation rate” in lower panels? Is that water vapor to cloud water, or water vapor to either water or ice? Please clarify.
12. I have to admit that I did not read and study figures beyond 13, but I find similarities between simulations applying the SBS and MOR schemes remarkable. This should be emphasized in the paper.
13. In view of my comments above, I do not agree with many statements in the concluding section 5, especially those related to cold and warm invigoration. I feel the section does not properly reflect results presented in the figures and is biased towards the authors’ view rather than what model results show. This has to change before the manuscript is accepted.