Review of “Precipitation Susceptibility of Marine Stratocumulus with Variable Above and Below-Cloud Aerosol Concentrations over the Southeast Atlantic” by Gupta et al.

This paper presents airborne observations from the ORACLES project that examine how cloud and precipitation characteristics vary with perturbations driven largely from the entrainment of free-tropospheric biomass burning aerosols into the southeast Atlantic marine boundary layer. The authors extend their previous study by incorporating a much larger observational dataset from additional flight years and they extend their prior work to look at precipitation susceptibility. I commend the authors for synthesising such a large dataset and I found the paper to be generally well written. The topic area is certainly suitable for publication in ACP. However, I do have a major concern about the use of the CAS probe to measure liquid water content and cloud drop size from the 2016 campaign (see below), that I feel the authors need to address before this paper can be published.

Main concern

1. Use of CAS probe for 2016 flights. I have concerns about the use of the CAS data for calculating microphysical properties on the 2016 campaign. Although the cloud drop number concentration from the CAS looks reasonable when compared against the PDI (Fig S1a), the LWC looks to be underestimated when compared against both the PDI and King probes (Fig S1b, Fig S2). The authors show that the PDI can give higher LWC values when compared to the adiabatic value and so choose not to use that instrument. But given that the bulk LWC estimate from the King probe is also much higher that the CAS (Fig S2), I think the authors need to provide some additional justification as to why the CAS probe is thought to be reliable (for measurements of LWC and effective radius). A possible approach would be to look at cases where the cloud was expected to be more adiabatic (well mixed boundary layer, non-drizzling etc) and examine if the difference with the adiabatic LWC value shown in Fig S2 is still apparent. Alternatively, in precipitating clouds, can the overlap with the 2DS probe be looked at to at least check for consistency at the larger cloud drop sizes that contribute significantly to LWC. I also note however that a similar low bias in LWC from the CAS is shown in the 2017 and 2018 campaigns when compared against a CDP (Fig S4 and S6), which suggests that it could be a general measurement issue with the CAS measurements. Related to this point, if the authors removed the 2016 data from their analysis, do any of the conclusions of the paper change?

Minor comments

1. Line 34: Suggest changing to “changes in microphysical properties” in this sentence as the proceeding sentence states that LWP and cloud thickness are similar. Also it is not clear what the reference to “existing relationships” means. Which relations are you referring to? Are these based on previous observations or parameterized/simulated in models for example?
2. Line 68: assuming constant LWP in what?
3. Line 78: sink of liquid water rather than LWP?
4. Line 82: Suggest changing to “relates the change in Rp….” as the actual definition is Eq 9.
5. Line 87: Suggest changing to “parameterized in models”
6. Line 93: Suggest changing to something like “A focus of recent field experiments in the southeast Atlantic Ocean has been to study ACI in this unique meteorological ……..”.
7. Line 98: I assume the values of single scattering albedo and above cloud optical depth are from ORACLES. Please make that clear. Much higher optical depths can occur in the region e.g. Peers at al. (2021).
8. Line 102: Suggest changing “positive forcing” to “aerosol absorption of SW radiation”. Also please expand on why this decreases entrainment e.g. strengthening inversion.
9. Line 149: Please include references for the different probes.
10. Line 159: Change to “Hawaii”
11. Line 165: What thresholds on the PCASP data were used to screen cloud?
12. Line 168: Change to “with the CDP N(D) for 50 < …..”
13. Line 170: Can the authors comment on how well the different probes compared for drop sizes where they overlap?
14. Line 176: refer the reader to the supplement.
15. Line 215: Please briefly outline what you mean by shallow boundary layers can provide an underestimate of LWP adjustments. And I don’t understand what you mean in the sentence on line 217. Please clarify.
16. Line 219: Have you done any analysis of the thermodynamic data to ascertain the frequency of well-mixed vs decoupled boundary layers from the vertical profiles used in this study? And are the clouds studied typically a single layer of stratocumulus, rather than cumulus rising into stratocumulus. If the latter form a significant number of profiles, can the authors comment on how that may impact the results e.g. cumulus could transport aerosol from the surface mixed layer up into the overlying cloud.
17. Equation 1: Is effective radius calculated as a function of height or is it a cloud top value.
18. Equation 4: What does LWC(zB) mean? Is it your fixed value of 0.05 g m-3 to define cloud base?
19. Line 283/Table 4: Is the effective radius calculated at cloud top, or is it an average value through the depth of the cloud?
20. Line 377: Suggest changing “ascent” to “updraft”
21. Line 385: Suggest changing “explained” to “parameterized”
22. Figure 5: y-axis labels should be SAUTO95 and SACC95
23. Line 420: Add comment as to why you use CO as a proxy for the airmass from biomass burning aerosol source regions.
24. Line 422: Suggest the authors may want to comment on how the different regimes occur. For example, does the S-H regime have high boundary layer aerosol loadings because of previous entrainment events prior to the aircraft sampling and does the C-L regime have low aerosol loadings because there hasn’t been sufficient time for aerosol to be mixed down into the boundary layer from the overlying aerosol plume.
25. Line 433: Figure 6 does not show comparisons of Re as stated in the text.
26. Line 443: The authors test boundary layer aerosol concentration thresholds of 300 to 400 cm-3 to split “low” and “high” aerosol conditions. Even the value of 300 cm-3 seems like a moderately polluted boundary layer though compared to pristine marine conditions, where I would expect values < 100 cm-3 to be typical. Did ORACLES measure cleaner boundary layer conditions and if yes, how do the cloud properties in these cleaner clouds compare to the broader “low” aerosol regime used in this study? Or do future studies need to compare/contrast with more offshore airborne measurements from the CLARIFY campaign for example?
27. Line 448: Is quartiles the correct term, given that the bins don’t have an equal number of profiles (82,80,85,82 in Table 6)?
28. Figure 9: It looks like there are data points with Nc = 0 cm-3. Is that correct?
29. Line 489: Suggest adding “decreased with H from …..include your numbers for the lowest H bin data….to 0.53”
30. I found some of the text hard to follow in section 6.3, that was at least in part due to the number of figures that were referred to in short succession. For example, the short paragraph beginning on line 489 refers to four different figures. I would suggest the authors consider rewriting some of the text and highlighting key points, to make it easier for the reader.
31. Line 491: I struggle to see how the reader can see this change by looking at Fig 9 b,c.
32. Line 513: The paragraph starts by mentioning appendix B, but does not then summarize the key point of that sensitivity study. Further, it states that the appendix investigates the inclusion of precipitating clouds, but I think it instead looks at the impact of the removal of non-precipitating clouds.
33. Line 600: What is the mechanism that results in higher RWP for these contact profiles?
34. Line 625: Suggest rephrasing this statement. The separated polluted boundary layers have presumably also experienced entrainment events prior to the aircraft sampling, even though there is no contact at the time of the measurements. The timescales of entrainment and history of the airmass do also need to be considered (Diamond et al., 2018), rather than just an instantaneous measure of “contact” vs “separated”.
35. Line 630: Make it clear that this is when compared to separated profiles.

References

Diamond, M. S., et al., 2018. Atmos. Chem. Phys., https://doi.org/10.5194/acp-18- 14623-2018, 2018.

Peers, F., et al., 2021. Atmos. Chem. Phys., 21, 3235–3254, https://doi.org/10.5194/acp-21-3235-2021.

• Does the paper address relevant scientific questions within the scope of ACP?
  • The paper addresses “Precipitation Susceptibility of Marine Stratocumulus” to variations in aerosol concentrations. This is an important topic within the scope of ACP.
• Does the paper present novel concepts, ideas, tools, or data?
  • The novel part of this research is the aircraft dataset. No new concepts, ideas or tools are introduced.

• Does the title clearly reflect the contents of the paper?
  • The title places emphasis on precipitation susceptibility, which is only a small component of the paper, has questionable validity, and lacks proper discussion.

• Does the abstract provide a concise and complete summary?
  • The title emphasises “Precipitation Susceptibility”. This is not mentioned at all in the abstract, but it is discussed in the conclusions.

• Are substantial conclusions reached?
  • The main results stem from figures 3 and 7, which demonstrate that there is some difference in the cloud microphysical properties between two subsets of the data. This is attributed to biomass burning aerosols entrained into the boundary layer from above. The paper also explores potential impacts of aerosols on precipitation formation, and the role of meteorological factors also affecting the microphysical properties. The conclusions are rather limited in scope, and in part unsubstantiated. I understand observational based research is important and also difficult to publish in its own right without complex modelling, so maybe a “Measurement Report” is more suitable format?

• Are the scientific methods and assumptions valid and clearly outlined?
• Are the results sufficient to support the interpretations and conclusions?
  • The paper uses specific statistical terminology (e.g. “95% Confidence Interval”) which inherently implies parameters are known to exhibit normal distributions when properly sampled. Is this valid? Is this approach needed?
  • Adiabatic approximations of Brenguier are used. Limitations should be discussed/quantified.
  • Measurement uncertainties are not presented alongside observations. E.g. What is the estimated uncertainty in measurements of droplet effective radius, and how does this relate to changes between cloud base/top, and also between the aerosol regimes studied?
  • Calculations in the paper suggest the thinnest clouds have large precipitation sensitivity to aerosols. This seems odd given these thin clouds have nominally the same droplet concentrations as thicker clouds, but only have the smaller droplets. This raises concerns with how data are handled and the overall validity of conclusions drawn from the analysis. From the text I don’t fully understanding what was done here with the data to determine the precipitation susceptibility, so maybe my interpretation is wrong, but I speculate it is a result of using outputs from regression analysis which are statistically meaningless. If this is true, the paper is presenting misleading results which is very undesirable. If this is not true it needs making clearer.
  • The stratiform clouds are shown to be around 200m thick, and often occur in the vicinity of convective clouds. Is direct comparison of high resolution in-situ datasets with relatively coarse resolution ERA5 reanalysis data sufficient to untangle effects of meteorology? What small-scale/local variations in SST could you expect based on other studies? What are the actual sizes/resolutions of ERA5 grid boxes in units relatable to the observations? Can ERA5 resolve the inversions etc? The correlations in Fig10b between LWP from in-situ and ERA5 are poor, which casts a large doubt over the validity over the in-situ LWP vs SST/LTS/EIS from ERA5. Why aren’t in-situ observations of inversion strength analysed?
  • From the very beginning this paper places emphasis on the role of aerosols from above cloud and their ability to modify clouds via entrainment etc. There is no discussion of the potential for the boundary layer being polluted with Biomass Burning aerosols in its own right, without the requirement for entrainment from above the BL inversion. Is there data showing the transition of the BL from clean to polluted as aerosol mix downwards? If so it would be very useful to show it.
  • The paper filters data according to aerosol concentrations above cloud (“contact” vs “separate” using a 500cm^-3 threshold) and below cloud (“high” and “low” Na with a threshold of 350cm^-3). However, the cloud droplet concentrations in Fig 6 do not show evidence of enhancement due to above cloud aerosols for the “clean” BL cases. The only strong response in droplet concentration is when there are lots of aerosols also in the boundary layer. It seems impossible to disentangle the below and above cloud aerosols and therefore the role of entrainment and above cloud aerosols is ambiguous.
  • There is no contextualisation of the results. For instance, are the calculated changes in re, or values of S_o “large” or “small”? Are changes in these clouds due to the Biomass Burning aerosols having any meaningful impact? What have other studies found?

• Is the description of experiments and calculations sufficiently complete and precise to allow their reproduction by fellow scientists (traceability of results)?
• Are mathematical formulae, symbols, abbreviations, and units correctly defined and used?
  • Undefined formulae: Z_N
  • Confusing presentation of Γ⁸⁵⁰_𝑚, in eqn 10
  • Description of LCL is confusing and the equation is poorly formatted
  • Some of the technical details of data processing are in figure captions, but should be included in the text.
  • What are the “kernel density estimates” mentioned in caption for Figure 3? They are not mentioned anywhere else in the paper.

• Is the overall presentation well structured and clear?
• Is the language fluent and precise?
• Should any parts of the paper (text, formulae, figures, tables) be clarified, reduced, combined, or eliminated?
  • The paper was difficult to follow. I feel the paper is too long and lacked coherence. It is very ambitious, and the authors have covered lots of areas which are all important and related, but the balance is not quite right. The paper has lots of useful data but in its current form does not provide concrete outputs which can be used by the broader community.
  • Most figures should be improved and are poorly rendered, and some do not have proper legends etc (e.g. Fig 10b has a 1:1 line listed as “x=y”, wrong coloured text in legends).

• Do the authors give proper credit to related work and clearly indicate their own new/original contribution?
• Are the number and quality of references appropriate?
  • Yes there are a good number of quality references. Some references are missing (e.g. description of instruments in section 2) but nothing major.

• Is the amount and quality of supplementary material appropriate?
  • Yes, supplementary material is of good quality and is a useful addition.