Cloud droplet formation at the base of tropical convective clouds: closure between modeling and measurement results of ACRIDICON–CHUVA

Braga, Ramon Campos; Ervens, Barbara; Rosenfeld, Daniel; Andreae, Meinrat O.; Förster, Jan-David; Fütterer, Daniel; Hernández Pardo, Lianet; Holanda, Bruna A.; Jurkat-Witschas, Tina; Krüger, Ovid O.; Lauer, Oliver; Machado, Luiz A. T.; Pöhlker, Christopher; Sauer, Daniel; Voigt, Christiane; Walser, Adrian; Wendisch, Manfred; Pöschl, Ulrich; Pöhlker, Mira L.

doi:https://doi.org/10.5194/acp-21-17513-2021

Articles | Volume 21, issue 23

Atmos. Chem. Phys., 21, 17513–17528, 2021

https://doi.org/10.5194/acp-21-17513-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

Atmos. Chem. Phys., 21, 17513–17528, 2021

https://doi.org/10.5194/acp-21-17513-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 21, issue 23

Research article

02 Dec 2021

Research article | 02 Dec 2021

Cloud droplet formation at the base of tropical convective clouds: closure between modeling and measurement results of ACRIDICON–CHUVA

Ramon Campos Braga et al.

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Final revised paper (published on 02 Dec 2021)
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Preprint (discussion started on 16 Mar 2021)
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Interactive discussion

Status: closed

RC1:
'Comment on acp-2021-80', Anonymous Referee #1, 13 Apr 2021

The manuscript compares measured cloud droplet concentrations with simulated values produced by a parcel mode. The manuscript lacks a significant amount of background information and information pertaining to the case studies in general. The main points of the article are either unclear, based on assumptions and at times drawn from similarities between cited other studies and not evidence.

The introduction takes a very general approach to providing background information. Including specific results and findings would help put your results into perspective. For example you indicated w has a large uncertainty, but how sensitive were previous studies shown to be sensitive to w? How does that sensitivity compare to other variables? How do past studies that used parcel models and equilibrium models compare? This information and other details from previous studies are necessary to understand the what is important and what assumptions are flawed. I suggest more work be put into including previous results that are relevant to your analysis.

A number of questions remain about the measurements used in the study. Why are the CDP and CAS droplet measurements so different? What measurements were actually used during the flight? Was the entire flight averaged? Were cloud edges excluded? Were the aerosol measurements collected relatively close to the cloud droplet measurements?

While the manuscript presents data from a valuable dataset, the analysis is not thorough, substantial amounts of detailed about the case study are missing and the conclusions are weak, and not evidence based. Based on my assessment, I suggest rejecting the manuscript.

Specific comments:

Line 69 - please define AC. It would be more useful for the reader to name the cases by their attributes than their flight number. Something like LPC- low particle concentration, MCP1,MCP2 –moderate particle concentration...etc.

Line 71- What do you mean by environment air? subsaturated air?

Line 73- By "at cloud base" do you actually mean at cloud base or was it slightly above or below cloud base?

Line 78 – where were these size distribution measurements made relative to the cloud measurments? Were they averaged before fitted to log normal distributions?

Line 80 – Please provide more detail on how the Aitken mode was inferred. It is unclear since the UHSAS only measured as low as 60 nm.

Line 91 – did you demean the updraft velocity? What do you mean by passes with only positive w were considered? Surely there were often some Negative values? I am guessing you mean you just excluded negative values?

Line 106 – Was there any drizzle in the measured clouds? It makes sense to exclude collision coalescence in a parcel model since it cannot be parameterized will with a 0D model, however can you confirm with measurements and results from previous modeling studies that Collision/coalescence are negligable in the clouds you studied (at least the lower 70 m).

Line 112 - "In order to determine the height at which Nd,m and Nd,p should be compared, simulations were performed using the measured aerosol particle size distributions and an assumed hygroscopicity of k= 0.1, together with w measured at cloud base." It is not clear how this I used to determine the height at which Nd,m and Nd,p should be compared.

Line 114- make it clear that this is a result from your adiabatic parcel model, not measurements.

Line 120 "in the following..." Section?

Line 133 – how do you define best agreement? Absolute concentration? Percentage difference?

Line 145 – For lateral entrainment to increase droplet concentration, the entrained concentration would need to be both CCN active and higher than the below cloud concentration. I have never seen a case where this has occurred. Can you cite a relevant source? Also, even if there was lateral entrainment, at altitudes so close to cloud base, it is unlikely that there is a significant influence from lateral entrainment. Entrainment would also likely dry the air, decreasing the supersaturation, further decreasing the chance of increasing the droplet concentration.

Line 147 – Entrainment typically leads to a decrease in Nd.

Line 150 – why is that unlikely?

Line 155- What evidence is there for this cloud being impacted by marine air? Having a bimodal distribution does not make an aerosol distribution impacted by marine air. It is very likely that all of the particle distributions have a bimodal distribution, however you cannot tell because you are limited to a minimum particle size measurement of 60 nm by the UHSAS. It is still unclear how you obtained an Aitken mode for AC19.

Line 157 – this result suggests that the aerosol you measured and the aerosol that entered the cloud are not from the same population.

Line 165 The following two quotes from your text are inconsistent with your argument "The chemical composition of Aitken mode particles often differs significantly from that of accumulation mode particles, which are more aged and internally mixed" "Marine particles often show similar hygroscopicity in both Aitken and accumulation modes"

Line 168 – You have indicated it is possible that the hygroscopicity of these particles may be inconsistent with the values you used because you think they are marine aerosol. You have the ability to test this hypothesis with your parcel model, but choose not to. Why?

Line 172- you should include sensitivity calculations.

Line 175- do you mean additional aerosol? Additional activation would surely lead to additional activated particles.

Line 178 – "high sensitivities of Nd to the chemical composition of Aitken mode particles might affect cloud properties" This statement is redundant.

Line 179 – comparable in composition? Concentration? This is unclear. This statement about kappa contradicts your statement in line 167.

Line 186- how was this 30% uncertainty calculated?

Line 215 – non-adiabatic conditions like entrainment would not increase particle concentration, only decrease.

Line 217 calculations are necessary to back this claim and could easily be performed.

Line 218 – you should be able to state your conclusions based on the evidence provided in the manuscript, not by citing others work.

Citation: https://doi.org/10.5194/acp-2021-80-RC1
- AC1: 'Reply on RC1', Mira L. Pöhlker, 02 Jul 2021
  
  The comment was uploaded in the form of a supplement: https://acp.copernicus.org/preprints/acp-2021-80/acp-2021-80-AC1-supplement.pdf
  
  Citation: https://doi.org/10.5194/acp-2021-80-AC1
RC2:
'Comment on acp-2021-80', Anonymous Referee #2, 16 Apr 2021
This manuscript showed closure results of measured and predicted cloud droplet number concentration for variable updraft speed during ACRIDICON-CHUVA campaign of 2014 where role of updraft speed, hygroscopicity and aerosol size distribution is discussed. Better closure results are obtained when k was assumed to be 0.1, updraft velocity is low and aerosol size distribution is unimodal. CCP and CAS-DPOL are used to measure cloud droplet size distribution and UHSAS with CPC for aerosol size distribution. Updraft speed is measured using Rosemount model 858 AJ probe. Overall the results could be a valuable contribution if they are backed up by proper justification. One of the major point of concern is the lack of reasoning when there is an agreement or disagreement in the closure results. It reads more like a report lacking scientific understanding of the results. I recommend the publication only if the authors improve the discussion part and add previous relevant studies for comparison and show why their approach is better than the earlier studies.

Specific Comments:

Line 66: Height of the cloud base?

Line 63-64: Purpose of using two probes: CCP and CAS-DPOL.

Line 84 and 186: How is the uncertainty of 30% is estimated?

Line 103: What will be the effect of size dependent hygroscopicity is assumed for external mixing state.

Line 133: Why there is a deviation between measured and modelled Nd at low w?

Line 129-130: What is the implication?

Line 105: Why collision and coalescence are not considered? Is there any measurement constraint or it is not important to consider?

Line 147: Under which specific conditions, there will be decrease of Nd due to entrainment of additional aerosols?

Line 155: Why is it assumed that bimodal size distribution is due to marine air? Are there any evidences of size dependent chemical composition?

Line 182-183: The sensitivity analysis of Aitken and accumulation mode to total Na and Nd should be included in this study as this is one of the highlight of this manuscript that represents scientific advancement.
Citation: https://doi.org/10.5194/acp-2021-80-RC2
- AC2: 'Reply on RC2', Mira L. Pöhlker, 02 Jul 2021
  
  The comment was uploaded in the form of a supplement: https://acp.copernicus.org/preprints/acp-2021-80/acp-2021-80-AC2-supplement.pdf
  
  Citation: https://doi.org/10.5194/acp-2021-80-AC2

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Mira L. Pöhlker on behalf of the Authors (02 Jul 2021) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (10 Jul 2021) by Markus Petters

RR by Anonymous Referee #2 (23 Jul 2021)

RR by Anonymous Referee #3 (16 Aug 2021)

Suggestions for revision or reasons for rejection

The main value of this work lies in the information offered from measurements of aerosol and cloud properties in fairly convective clouds in an interesting location.

1) The main objective(s) of this paper are unclear:
a. The title indicates closure, but reasonable closure is not possible here for two reasons. One is that there are two measurements of cloud droplet number concentrations that are separated by 20-30% before considering the uncertainty in the measurements. The second reason is that there is no independent estimate of kappa. With the information presented, the model is incapable of producing closure because it is the comparison of the model and observations that is used to estimate the best kappa. This implicitly assumes that the other observations are correct, but we know that is not the case because the two Nd measurements disagree. I am not being critical of the Nd measurements: I applaud the authors for including both. My suggestion is to take your best case, in terms of measured quantities, including information available to define kappa, and attempt closure of the model with the two measurements of Nd. Your best case might be the simplest, and the one that has the best estimate of updraft speed or w; more discussion of w later. The objective of this best case would be to be able to say something about how the two measurements relate to the modelled Nd.
b. In the abstract and later in the text, there is considerable discussion of the best kappa value. I don’t see this as a major objective of this paper. There are better ways to estimate kappa, which the authors refer to, than to use such a convoluted approach that incudes uncertainties. Use estimates of kappa from previous studies in the region.
c. The last sentence of the abstract says that “Our results indicate that Aitken mode particles and their hygroscopicity can be important for droplet formation at low pollution levels and high updraft velocities in tropical convective clouds.” This seems like a result worthy of publication, if the authors first acknowledge previous related work: Leaitch, W. R. et al., Effects of 20–100 nm particles on liquid clouds in the clean summertime Arctic, Atmos. Chem. Phys. 16, 11107–11124 (2016); Baccarini et al., Frequent new particle formation over the high Arctic pack ice by enhanced iodine emissions, Nature Comm. https://doi.org/10.1038/s41467-020-18551-0, 2020.
d. The last sentence of Section 1 tells us that the modelling is used to examine the sensitivities of Nd to kappa, Na and w, but we’ve been subjected to such sensitivity studies for many years now, dating back to at least 1971 (Junge and McLaren, JAS, 1971), which told us that the number distribution was more important than the chemical content of the particles. Why is another sensitivity study of this important?

2) Lines 42-50: Leaitch et al., Cloud albedo increase from carbonaceous aerosol, Atmos. Chem. Phys., 10, 7669-7684, 2010 is relevant here.

3) Line 93 – What is the Aerosol Measurement System, and why do we need to know its acronym?

4) Lines 104-106 – Your inferred Aitken distribution has a minimum at about 80 nm, based on the Wex, Gong and Quinn distributions. The below-cloud distributions measured over the North Atlantic Ocean by Leaitch et al. (ACP, 2010), also used in parcel model calculations, had minima at about 100 nm. Such a minimum might make a substantial difference in your results, for example, potentially requiring a smaller kappa for the Aitken mode.

5) Lines 118-126 – Are the differences in the sampling approach by the CAS and CCP potentially responsible for the bias in the two measurements?

6) Lines 131-133 – Given the better agreement with the King probe, why were the CAS measurements not chosen to compare to the model alone? Were number or sizing differences mostly responsible for the differences between the CAS and CCP probe comparisons with the King probe?

7) Section 3.1 –
a) It would be helpful to have an example of the time series of Nd and w during a cloud penetration to demonstrate the application of this approach here. By design, the PMM analysis appears to ensure the connection between Nd and w shown in Figures 3 and 4, whereas other methods, such as Peng that you later refer to as weaker (Lines 339-345), do not. Because of the apparent forced dependence by the PMM method, it seems inappropriate to use this approach to make conclusive statements about the dependence of Nd on w.
b) The Peng approach, and perhaps others, were developed for stratus and stratocumulus with relatively low updraft speeds. The pathways of air parcels through such clouds, as shown by modelling studies (e.g., at CSU), are much different than for more convective clouds, and therefore the Peng approach may not be appropriate here in any case. For strong convection, the w may significantly increase with height above cloud base. How do you know that your w, measured more than 20 metres above base, were indeed representative of the w at cloud base? The Nd may not change much with height (assuming only homogeneous entrainment), but the w can, and based on the LWC shown in Figure 2 sampling was conducted well above cloud base in many cases, which would lead to overestimating w in some cases.

8) Line 190 – Unless there is some inhomogeneous mixing.

9) Lines 207-208 - Curious statement: effectively, you are saying that variations in Nd of 20-40% aren't large enough to worry about. Is that the status of the indirect effects?

10) Lines 209-211 - This statement is predicated on the correct answer lying between the two measurements, yet there is nothing in the paper to suggest that is correct.

11) Lines 219-220 – “Confirm” is an exaggeration. It could be true, but you haven’t demonstrated this, and there are better ways to estimate kappa. This approach is too uncertain.

12) Lines 222-225 – If you sampled very near cloud base, then it would seem difficult for entrainment to increase the Nd. Again, it is important to illustrate your in-cloud selection process. If you sampled too high above cloud base, then you need to question your estimate of w. Also, your statement here is incorrect if the CCP measurements of Nd are closest to reality. Overall, I don’t find this paragraph useful.

13) Lines 231-235 – When you say the hygroscopicity of particles could change due to dissolution of soluble compounds, do you mean the uptake of highly soluble gases, such as HNO3? If so, a reference is in order: Kulmala et al., maybe JGR, in the 1990s. If you are talking about delays associated with weakly soluble compounds, then Shantz et al.: Effect of organics of low solubility on the growth rate of cloud droplets, J. Geophys. Res., 108, 4168-4177, 2003 is appropriate here and on line 405. Your assumption that reduced solubility might flatten the curves more may or may not be correct, depending on the entire chemical composition of the size distribution. Shantz et al found that delayed growth reduced the Nd relative to a highly soluble compound. I don’t see enough support for your statement that “such composition effects can likely be excluded.”

14) Lines 236-237 – Yet, your Aitken mode is highly soluble.

15) Lines 338-247 – Again, I suggest that your tendency of measured Nd vs w is at least in part a result of your approach.

16) Line 274 – Nd to Na?

17) Lines 350-353 – “we conclude that the sensitivity of Nd to Na is much greater than that to w under these conditions which is also reflected by the rather small increase in Nd with w at high updraft velocities”. Again, we need to know where with respect to cloud base that the w were measured, in case some of your w are overestimated.

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ED: Reconsider after major revisions (17 Aug 2021) by Markus Petters

AR by Mira L. Pöhlker on behalf of the Authors (14 Sep 2021) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (16 Sep 2021) by Markus Petters

RR by Anonymous Referee #3 (29 Sep 2021)

Suggestions for revision or reasons for rejection

Please consider the following comments:

1- Authors’ response to my original comment 1): “We respectfully disagree that the term ’closure’ is not appropriate here. We refer to the definition of ’closure’, as described in previous studies, e.g., by Quinn and Coffman (1998): "In a closure experiment, an aerosol property is measured by one or more methods and calculated from a model that is based on other independently measured properties. A comparison of the measured and calculated values can reveal inadequacies in either the measurements or the model." Even the aforementioned study did not focus on cloud droplet number concentration, generally this definition is very well in agreement with our approach.”

Review comment on this response: - Of course, I agree with the stated reference as to the nature of closure. Unfortunately, I find this statement to reinforce my point, rather than the authors. You have not measured kappa by any methods. You use the model to make an assessment of kappa, but you cannot call it closure because you do not have anything to give you an independent assessment of kappa to compare against.

2- Authors’ response to my original comment 1 b): “The referee is right that indeed there are more straightforward ways to estimate kappa but most of them do not use data from real cloud bases for such a broad range of conditions as we did.”

Review comment on this response: Why would there be a difference between estimating kappa below a cloud rather than not below a cloud? Effects on photochemistry might play some role, but I don’t see how your results that show a range of kappa values is either better or for that matter distinguishable from an approach that offers a more direct estimate of kappa, whether below or not below a cloud.

3- Authors’ response to my original comment labelled 1c: “Since the conditions in the Arctic are substantially different to those in our current study in terms of aerosol loading, w and CCN-limited regime, we did not add the references to the manuscript.”

Review comment on this response: This is about processes, not location. The relative importance of the many relevant processes may vary from one location to another, but in this case one of the most important factors is the effect of “aerosol loading”. Low concentrations of larger particles are the main reason Aitken particles can activate in the Arctic. As for updrafts, if particles as small as 20-30 nm can activate in the Arctic, then it is more likely to happen in cases of higher updrafts. These references support your work here, and they are warranted.

4- In response to review comment 7b), the authors state: “we could not ascribe a specific
height for measurements of cloud bases but rather state that they had approximately the same altitude during the cloud passes”.

Review comment on this response: Thank you for Figure R2-1. You should be able to calculate an approximate distance above cloud base based on the size of the droplets using your adiabatic parcel model. LWC is dependent on height above base, not updraft speed, so you just need to define the activated number concentrations and see at what heights you reach your measured diameters. You don’t even need a lot of sophistication, and this will offer a better estimate of height above base.

5- In response to review comment 14 (“Yet, your Aitken mode is highly soluble”), the authors state that they have no information on the solubility of Aitken mode particles. On lines 259-261 of the revised paper, they state that “Even assuming rather extreme values of kappaAit = 0.8 cannot fully reproduce the large increase in Nd at w & 1.5 m s-1 as observed by the CAS probes; assuming very hygroscopic Aitken mode and less hygroscopic accumulation mode particles can approximately reproduce the trend in Nd,m from the CDP.”

6- Review comment 15 – The authors acknowledge that the approach they use to associate Nd and updraft speed reinforces a strong correlation. In other words, the approach is not entirely objective. This should at least be discussed somewhere in the paper.

7– I do applaud including both measurements of Nd, but I feel that one is likely to be closer to the truth than the other, and I think this could be assessed.

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ED: Publish subject to minor revisions (review by editor) (29 Sep 2021) by Markus Petters

AR by Mira L. Pöhlker on behalf of the Authors (04 Oct 2021) Author's response Author's tracked changes Manuscript

ED: Publish as is (04 Oct 2021) by Markus Petters

Short summary

Interactions of aerosol particles with clouds represent a large uncertainty in estimates of climate change. Properties of aerosol particles control their ability to act as cloud condensation nuclei. Using aerosol measurements in the Amazon, we performed model studies to compare predicted and measured cloud droplet number concentrations at cloud bases. Our results confirm previous estimates of particle hygroscopicity in this region.