Observational constraints suggest a smaller effective radiative forcing from aerosol–cloud interactions

Park, Chanyoung; Soden, Brian J.; Kramer, Ryan J.; L'Ecuyer, Tristan S.; He, Haozhe

doi:https://doi.org/10.5194/acp-25-7299-2025

Articles | Volume 25, issue 13

https://doi.org/10.5194/acp-25-7299-2025

© Author(s) 2025. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/acp-25-7299-2025

© Author(s) 2025. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 25, issue 13

ACP Letters

| Highlight paper

|

14 Jul 2025

ACP Letters | Highlight paper |

| 14 Jul 2025

Observational constraints suggest a smaller effective radiative forcing from aerosol–cloud interactions

Chanyoung Park, Brian J. Soden, Ryan J. Kramer, Tristan S. L'Ecuyer, and Haozhe He

Download

Final revised paper (published on 14 Jul 2025)
Supplement to the final revised paper
Preprint (discussion started on 03 Sep 2024)

Interactive discussion

Status: closed

CC1:
'Comment on egusphere-2024-2547', Erin Raif, 16 Oct 2024
This comment is a joint review created as part of EGU’s Peer Review Training Workshop 2024. The reviewers were Erin Raif (University of Leeds), Piotr Markuszewski (Institute of Oceanology Polish Academy of Sciences) and Sebastián Mendoza-Téllez (Universidad Nacional Autónoma de México).
In this paper, the authors used a combination of satellite observations and model reanalysis data to constrain the contribution to effective radiative forcing from aerosol-cloud interactions (ERFaci) in low clouds. In doing so, the authors suggest that previous estimations overestimate ERFaci. They also find that the activation rate of aerosols into cloud droplets must be considered to reduce the uncertainty on effective radiative forcing.
This is an interesting hypothesis with important consequences for the calculation of cloud feedbacks. The data used is comprehensive, the analysis is thorough and the figures are largely clear. However, there is limited discussion placing this work into the context of works that have preceded it, and the importance of the results is not fully explored. Additionally, there are significant issues with the structure of the paper, which does not conform to a typical ACP structure and at times impedes comprehension of the content.
As such, we jointly recommend that this paper be reconsidered after major revisions.
Major comments:
The authors provide excellent detail to many aspects of their methodology. However, this should generally be contained within the main body of the paper, with only aspects that are unnecessary for comprehension of the methods remaining in the appendices. Additionally, the current structure of the methods/appendix means it is difficult to understand how the individual components fit together – we suggest that the authors a) add a short summary at the start of the new methods section to introduce them; b) explicitly discuss how their cloud-controlling factor analysis compares to the approach of Wall et al. (2022) and c) clearly introduce each data source to help readers familiar with either satellite or reanalysis methods only.

While the authors have done an good job of explaining their own approach, there is little discussion as to how this compares to previous work in the field. This leads to two key issues which should be addressed by further discussion of existing literature. a) It is difficult to establish from the introduction how ERF_aci is currently estimated, why this approach is limited and how this work differs from those previous approaches. b) Reading the discussion and conclusion, it is difficult to establish the relative importance of these new results that the abstract implies. Similarly, it is also difficult to understand the limitations of this approach.

The results and discussion may be better separated, or at least delineated further with some discussion of each result followed by section for discussion of the results in synthesis.

If appropriate, it would be useful to present p-values alongside r-values throughout the paper to improve the statistical rigour of the findings.

Minor comments:
Line 34: The authors should consider providing a definition of radiative forcing while still early in the introduction to the paper.
Lines 34-36: Not all aerosols act to reduce precipitation and increase cloud liquid water path. For instance, ice-nucleating particles initiate ice formation, which has the opposite effects (though these are unlikely to affect tropical low clouds).
Line 49: “the conventional assumption is that…”. It would be useful to know who makes this assumption.
Line 51: Is there a reference that justifies the "one-to-one aerosol cloud relationship" argument? [see also comments re. lines 70 and 80]
Line 66: Can the authors here explicitly summarise the main focus of the “story” by presenting a research hypothesis or clear research questions?
Lines 70-74: This goes some way to answering the comment on line 51, so should probably be moved to the introduction. However, further expansion may also be helpful for the reader – why is the assumption of a 1-1 ratio wrong?
Line 80: The relative strength of the relationship in different regions is very interesting. In most regions, the relationship is proportional but not one-to-one. Could the authors clarify why this might not be expected, as SO4 is only a subset of aerosol?
Figure 1: We think the interpretation of the plot is good. Can correlation coefficients of 0.4 be described as highly linear?
Line 113: Eq. 1 implies there are ten states that LWP can be in. Can the authors clarify what they mean by this, and perhaps briefly detail them?
Figure 2: The difference in meanings between panels (b) and (c) and panels (d) and (e) could be clarified by adding description to the colourbar adjacent to plot (c).
Line 179-188: In Figures 3a and 3c, the authors clearly show the ensemble ERF_aci is improved by considering activation rate. However, there are similar absolute numbers of models which perform well regardless of the treatment. Are these the same models in each case, and if so, is there an indicator as to when considering activation rate is important to capture ERF_aci and when it is not?
Line 200-201: “…our estimates offer further evidence to support estimates on the lower end of [the WCRP’s] range”. This seems to contradict Fig 4, where the red bars indicating ERFaci_obs have the largest values. Do the authors mean to say less negative?
Line 202: Could the authors clarify what a “top-down” approach is and how it differs from their analysis?
Line 220: What threshold was chosen for models to fall into the GOOD HIST category?
Figure 5: We assumed that, like other plots, the solid dots referred to values obtained when activation rate was considered. However, it would be useful to specify this in the caption. Additionally, there is no colourbar – we think this is because the colours correspond exactly to the x-axis. If this this the case, consider removing the colours as it implies an extra variable (such as each colour representing a different model) and the yellow unfilled circles are difficult to see.
Line 247: For readers who are reading the paper non-linearly, consider specifying the degree to which the influence of aerosols may be less substantial than assumed.
Line 335: Does the choice of a 50 year period remove interannual variability or reduce the influence of it? And if so, relative to what?
Line 335-337: Was there a specific reason why the 13 and 9 models were chosen for SO4 and AI respectively?
Line 370: To make this clearer for the reader, consider ending this sentence with e.g. “in this case, SO4 concentrations or AI”.
Line 403: What is the 1pctCO2 scenario?
Line 437: Consider using “more negative” rather than larger.
Line 457: Is there any literature to back up the assertion that the polar oceans will not contribute largely to the ERF_aci?
Line 477: Consider a section title that is more specific than “Uncertainty”.
Table A1: Please add more detail to the caption, such as what the circles mean and brief redefinitions of the variables.
Technical corrections:
Throughout: the authors should consider when to italicise and when to romanise variables and subscripts in equations, which is discussed in the ACP guidelines (https://www.atmospheric-chemistry-and-physics.net/submission.html#math)
Line 14: replace “it is assumed” with “assume”.
Line 39: ERFaci has not yet been defined in the text, just in the abstract, so this should precede the abbreviation.
Figure 1, line 794: add the word “hatching” after diagonal.
Figure 1, line 796: “stippling” might be my new favourite word!
Figure 1, line 797: “Stduent’s” should be “Student’s”.
Line 326: The sentence beginning “So, the models…” is a clause that doesn’t form a full sentence. Consider a change such as “This suggests that the models…”
Line 491: delete the second instance of the word “the” in the phrase “hence Cii represents the diagonal components of the C”.
Lines 521 and 530: these are quite unwieldy and should probably be standalone equations.
Citation: https://doi.org/10.5194/egusphere-2024-2547-CC1
- AC3:
  'Reply on CC1', Chanyoung Park, 04 Dec 2024
  
  Thank you Erin Raif, Piotr Markuszewski, and Sebastián Mendoza-Téllez for your constructive comments. We have addressed your feedback in the attached file.
  
  Citation: https://doi.org/10.5194/egusphere-2024-2547-AC3
  - AC6: 'Reply on AC3', Chanyoung Park, 04 Dec 2024
    
    Please see the attached document for our corrected responses.
    
    Citation: https://doi.org/10.5194/egusphere-2024-2547-AC6
RC1:
'Comment on egusphere-2024-2547', Anonymous Referee #1, 25 Oct 2024

The article "Observational Constraints Suggest a Smaller Effective Radiative Forcing from Aerosol-Cloud Interactions" by Park et al. quantifies the effective radiative forcing from aerosol-cloud interactions to better represent climate predictions. The authors used satellite observations, reanalysis and climate models to support their analysis and results, and they focus on the effect of aerosols on cloud droplet concentration and evaluate the role of aerosol activation, which is usually overlooked in current estimates of effective radiative forcing.

I think this topic is within the scope of the ACP, as it seems to be an important parameter that the scientific community should take into account. The hypothesis is well explained and we understand each step of the process, but there are parts that should be improved before publication on ACP. I think the main problem is the predominance of the appendix and important information should be included in the main article. I am also concerned about the omission of meteorological parameters in the study and I do not know how this affects the study of cloud controlling factors. I recommend the paper for publication after the major revisions I suggest below.
Major Comments

1. The conclusion does not follow the ACP recommendations. The conclusion needs to be expanded.

“Every article must have a final section where the overall advances are concisely summarized and put in context. Although the results section may include some discussion, a synthesis and interpretation must appear in the final section. ACP expects that the concluding section will normally include the following components, although not necessarily in separate paragraphs:

* Summary: Summarize the main results and relate them to the objectives, questions, or hypotheses of the study. The summary should include the main quantitative results.

* Synthesis/interpretation: Explain and interpret the results concisely to enable readers to make sense of them as a whole.

* Comparison and context: Compare the results with previous studies to put them in context. Explain consistencies, inconsistencies, and advances in knowledge.

* Caveats and limitations: State how these affect confidence in the overall results, and where future work is needed.

* Implications: Discuss what the results mean for our understanding of the state and/or behaviour of the atmosphere and climate, which is the main requirement for publication in ACP. The editor's acceptance/rejection decision will be strongly guided by this component of the concluding section.”
2. Aerosols have an effect on cloud properties, cloud droplet size and droplet concentration, but the effect is small compared to the effect of meteorological parameters. If the authors did not constrained the results of Fig. 1 by meteorological parameters, then the changes in Nd can be due to meteorological parameters and what is observed is (indirectly) the correlation between aerosols and meteorological parameters. If I understand correctly, these coefficients are used afterward in the Equation A6. This problem is taken into account for the cloud controlling factors but I am not sure about the impact for the study.
3. Section A3 : Cloud controlling factor analysis,

Have the authors attempted to perform a Variance Inflation Factors analysis to estimate the performance of the CCF (as done in Scott et al. 2020) to avoid any cross-correlation and ensure that the effect seen is due to aerosols only?
4. L457: The authors state that their value is the same as the global value because the polar ocean surfaces are limited in area. Firstly, we can argue whether the region is indeed negligible in terms of area compared to the globe, but their impact could be significantly greater in these regions due to their specificities (polar night/day, ice surface, pristine conditions…). I am currently not convinced that the results can really be generalised to the globe.
5. A3, have the authors considered different cloud regimes as in Scott et al 2022 ?
6. Statistical tests and quantification would be welcome to better assess the results instead of “significantly diminishes” for example, etc.
Minor :

The ACP guidelines mention : “Appendices: all material required to understand the essential aspects of the paper such as experimental methods, data, and interpretation should preferably be included in the main text.” I have found that most ACP papers have data set and methods sections and usually an appendix with important information. I strongly recommend to include the data set and method sections in the main body of the paper and not in the appendix, following the ACP recommendations.
L14: “While some studies it is assumed”, I suggest “While some studies assumed”
L15: “Variation in sulfate aerosols”, do the authors mean sulphate aerosol concentration? It could also be aging, coating, etc that would change the aerosol-cloud interaction.
L15: I think Sulfates are SO42- and not SO4
L20: It would be interesting to know how much, on average, the ERF is reduced and less uncertain. A quantification would increase the impact of the abstract.
L34: All aerosols do not act as CCN, some would act as INP, and some would not interact with clouds.
L47-51: Citations are missing to support the text.
L62: Have the authors constrained to consider situations where sulphate aerosols are the dominant aerosol type (e.g. more than 80% of the total concentration?) Other aerosols may not be as efficient CCN but they could still bias their results.
L77: I do not think Nd is defined in the paper.
L81: I would not expect a one-to-one relation. As the authors mentioned it is related to the activation rate but this would mean that SO4 is the only CCN.
L82-84 : “show a notably weaker (…) coefficient”, bur the correlation coefficient, therefore shall we conclude anything from that ?
Fig1: I am not sure what is the date range used by the authors to produce the plot.

L85: I do not find the results consistent between AI and SO4, there are negative values and the results with large regression coefficients are not the same. Can the authors clarify what they mean by consistent?
L201 : “lower end”, Do they authors mean “higher end” ?
Equation A1: I am not sure to understand the equation, Ln is at the 2.5 horizontal resolution but L and U are at the native resolution but within the 2.5 degree grid cell, is it correct ?
Equations A5 and A6, what is needed to account for LWP bins? If I understand, the authors have constrained for LWP, is 30 g cm-2 bins sufficient? Have they tried smaller bins to see how the results change?
L558 and L561, I cannot access the webpages:

https://esgf559node.llnl.gov/projects/cmip6/ and https://github.com/nicklutsko/Radiative_Forcing_Aerosol_Clouds
I think all the appendices are not referenced in the main text. For example, I cannot see where sections A3 and A4 are referenced in the main article. It just says "In Appendix A". Again I think most of the part should be in the main text but for the remaining part, I suggest to clearly specify which part is referenced in the main text.

Citation: https://doi.org/10.5194/egusphere-2024-2547-RC1
- AC1:
  'Reply on RC1', Chanyoung Park, 04 Dec 2024
  
  Thank you RC1 for your constructive comments. We have addressed your feedback in the attached document.
  
  Citation: https://doi.org/10.5194/egusphere-2024-2547-AC1
  - AC4: 'Reply on AC1', Chanyoung Park, 04 Dec 2024
    
    Please see the attached document for our corrected responses.
    
    Citation: https://doi.org/10.5194/egusphere-2024-2547-AC4
RC2:
'Comment on egusphere-2024-2547', Anonymous Referee #2, 29 Oct 2024

Observational Constraints Suggest a Smaller Effective Radiative Forcing from Aerosol-Cloud Interactions
Park, C., et al
General Comments:
The paper uses models and observations to evaluate assumptions made in the determining aerosol-cloud interactions. Specifically, the authors argue that assuming a one-to-one relationship between activation rate of cloud droplet number concentration in response to sulfate aerosol variations and effective radiative forcing by aerosol-cloud interactions (ERFaci) leads to an underestimation of ERFaci. The corroborate this by performing a “perfect-model” validation comparison between climate model “true” ERFaci and that obtained via the aforementioned assumption. They compare observationally constrained ERFaci with previous estimates and conclude that ERFaci may be smaller than previously estimated.
The paper is acceptable with minor revisions (see below). It would be helpful if the authors provided readers with a sense of how widespread the above one-to-one assumption is used in prior studies (e.g., by providing references).
Specific Comments:
Lines 48-51:”The conventional assumption is that the activation rate has a one-to-one relationship when aerosols convert into cloud droplets and is typically not explicitly incorporated into the estimation process of ERFaci.”

Awkward sentence. Please reword. Also, please provide some references where the “conventional assumption” is used.

Line 73: “This ratio, commonly referred to as the activation rate, quantifies the efficiency with which aerosol particles convert into cloud droplets.”

Is a constant ratio assumed everywhere? If so, please state this and provide the assumed value.

Line 78: “Figure 1”.

Please consider using a different color scale. It’s not easy to decipher the values when only red is used.

Line 87: “The relatively low correlation coefficients observed for…”

Do you mean regression coefficient?

Lines 279-280: “Specifically for sulfate aerosols, it employs bias-corrected observations of total aerosol optical depth in conjunction with…”

Please state where the total aerosol optical depth observations are from.

Citation: https://doi.org/10.5194/egusphere-2024-2547-RC2
- AC2:
  'Reply on RC2', Chanyoung Park, 04 Dec 2024
  
  Thank you RC2 for your constructive comments. We have addressed your feedback in the attached file.
  
  Citation: https://doi.org/10.5194/egusphere-2024-2547-AC2
  - AC5: 'Reply on AC2', Chanyoung Park, 04 Dec 2024
    
    Please see the attached document for our corrected responses.
    
    Citation: https://doi.org/10.5194/egusphere-2024-2547-AC5

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision | EF: Editorial file upload

AR by Chanyoung Park on behalf of the Authors (04 Dec 2024) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (04 Jan 2025) by Timothy Garrett

RR by Anonymous Referee #1 (31 Jan 2025)

Suggestions for revision or reasons for rejection

1. I had a concern about the layout and structure of the article with most of the technical information (data and methods) in the appendix. I am still confused and compared to the letter format of other journals, there is more information on data and methods in them. I am not familiar with ACP letters, so I leave it to the editor to decide if there is enough information in the main article.

2. I am still confused about the extension to the whole domain. It is still based on a hypothesis and the article is not very clear about this (or I miss the sentence). I agree with the authors that sulphate mass concentrations are mainly concentrated in major industrial regions, but the Arctic regions have shown that the effect of aerosols acting as CCN is particularly efficient in the Arctic (up to 8 times more efficient compared to mid-latitudes, see coopman et al., 2018).
Coopman, Q., Garrett, T. J., Finch, D. P., & Riedi, J. (2018). High sensitivity of arctic liquid clouds to long-range anthropogenic aerosol transport. Geophysical Research Letters, 45, 372–381. https://doi.org/10.1002/2017GL075795

3. I disagree with the authors about the convention of referring to SO42- as SO4 and think it should be changed throughout the text. I agree that SO4 could be clear to readers, but I do not think it is correct to write it in this way. I will follow the editor decision with this matter.

4. I still have concerns about using only SO4 as an aerosol. On line 110 of the manuscript, the authors state that it is 64% smaller with activation than without. Taking into account other aerosols might potentially diminish the difference. The information with the AI is more impactful in this regards.

5. Some of the texts in the appendix are referenced in the main text : Appendix A, A1.2, A1.1 for example.

Hide

ED: Reconsider after major revisions (04 Feb 2025) by Timothy Garrett

AR by Chanyoung Park on behalf of the Authors (25 Feb 2025) Author's response Author's tracked changes Manuscript

ED: Publish subject to minor revisions (review by editor) (13 Mar 2025) by Timothy Garrett

AR by Chanyoung Park on behalf of the Authors (20 Mar 2025) Author's response Author's tracked changes Manuscript

ED: Publish as is (29 Mar 2025) by Timothy Garrett

ED: Publish subject to minor revisions (review by editor) (04 Apr 2025) by Ken Carslaw (Executive editor)

I am reviewing your paper for the first time in order to decide whether it qualifies as a Letter. Before accepting it as a Letter rather than a regular article I would like to see some appreciation that the approach you have taken to estimating ERFaci is only one of several others. Satellite estimates of dNd/dSO4 is one metric, but several other studies have applied multiple constraints simultaneously and reached different conclusions. Reliance on one or a small number of constraints can lead to over-constraint, which I am concerned may be the reason for the overly tight constraint that you present. For example, just from my own group's work (see eg https://acp.copernicus.org/articles/23/8749/2023/ and references), we use dozens of constraints in a statistically rigorous approach that accounts for potential model structural biases and conflicting observations. Ignoring conflicting constraints can lead to over-constraint, which is a well-understood problem with the emergent constraint approach for example.
To be acceptable as a Letter I would like to see some recognition of this issue. In particular, it's important to make clear that the tightness of your constraint is inconsistent with other approaches in which a larger number of constraining observation types are used. In addition to citing some of the other studies using different approaches, it is important to point out that your tight constraint applies to the _particular_ approach that you have used. It therefore is a major revision to studies that have used this same particular approach (you cite 4 such studies), but not those that have used alternative approaches. Based on those alternative approaches, a larger uncertainty range remains plausible. It should be made clear that this discrepancy in the tightness of constraint remains to be resolved.
My assessment above draws comparisons with my own group's studies, but there are others, and you should not see my comments as an attempt to seek citations, but rather to make the novelty of your study a bit clearer.

Hide

AR by Chanyoung Park on behalf of the Authors (08 Apr 2025) Author's response Author's tracked changes Manuscript

ED: Publish as is (15 Apr 2025) by Ken Carslaw

ED: Publish as is (15 Apr 2025) by Ken Carslaw (Executive editor)

AR by Chanyoung Park on behalf of the Authors (15 Apr 2025) Manuscript

Download

Article (4805 KB)
Full-text XML

Executive editor

Before acceptance of this preprint as an ACP Letter, as Executive Editor I requested that the authors clarify that that the approach they have taken to estimating ERFaci is only one of several others. Several other studies have applied multiple constraints simultaneously and reached different conclusions about the tightness of constraint. Reliance on one or a small number of constraints might lead to over-constraint, which I was concerned may be the reason for the overly tight constraint that is presented. In particular, ignoring conflicting constraints can lead to over-constraint. I requested that the author make clear that the tightness of constraint is inconsistent with other approaches in which a larger number of constraining observation types are used. Based on those alternative approaches, a larger uncertainty range remains plausible. Based on the added text drawing comparisons with previous similar and alternative studies, I am happy to accept it as a Letter based on the novelty and advancement in our quantification of aerosol radiative forcing.