Review of egusphere-2025-4169

General Comments

This study examines uncertainties in the most widely used remote sensing retrievals of droplet number concentrations and their implications of albedo susceptibility calculations, which are a core part of the analysis of aerosol cloud interactions and highly relevant to our understanding of climate. The authors make a valuable novel contribution in this study by using Large Eddy Simulations and 3D radiative transfer (3DRT) models and so can provide end-to-end analysis of errors. They also claim to have analysed albedo susceptibility but there are significant flaws in this analysis for which I recommend major revisions. I believe that once these are addressed that this article will make a valuable contribution to ACP.

Specific Comments

“ACI analysis” in the title & abstract etc. is far too broad for what is covered in this paper. This should be narrowed to “albedo susceptibility estimates”.

1. Anisotropy & Flux:

Here, I will be blunt, if only to impress upon the editor the importance of the issues I raise. This study neglects the anisotropy of radiation while making claims about a radiative flux (and its susceptibility) in Section 2.4. There is also a lack of a reference calculation of albedo susceptibility (discussed further below). These omissions render the results in this section largely meaningless.

A large part of the 3DRT effect on TOA irradiances is changes in the anisotropy of radiation with optical depth. For example, for near overhead sun, nadir reflectance saturates more quickly for finite clouds (e.g., a cube) than the oblique views. In other words, the angular pattern of the susceptibility changes from 1DRT to 3DRT. The effects of 3DRT on albedo susceptibility cannot be estimated while neglecting the anisotropy of radiation. The burden of proof is on the authors to demonstrate that the anisotropy susceptibility is unimportant for their analysis.

This study presents several different estimates of albedo susceptibility and compares them in Section 2.4. For example, a 1DRT+regression estimate applied to measurements generated using 1DRT and measurements generated using 3DRT (at 100 m or 800 m resolution) are compared. None of these four estimates are the truth and so it is not possible to tell whether agreement between estimates indicates good or poor performance. Without a clear reference, this makes it easy for a reader to come to an incorrect conclusion about what these results imply about the accuracy of using 1DRT to estimate albedo susceptibility.

The derivative of TOA albedo (averaged over some reference area) with respect to optical depth in each column has an exact expression in terms of linearized 3DRT (Doicu and Efremenko, 2019) that should be used as the reference for evaluating all approximations of albedo susceptibility.

These elements need to be present or other supporting evidence included to justify the claims presented here. Either the claims about the efficacy of estimating albedo susceptibility using 1DRT need to be removed or appropriate evidence needs to be added.

I note that the calculation of reference-quality albedo susceptibility will require a greater application of technical effort and computational power than the entire contents of the manuscript, which is why I suggest that it be removed.

Other specific flux issues:

Line 211-212: CERES is an estimate of F_3D, it is not measuring a fundamentally different quantity. Yes, there will be errors. By construction an empirical ADM method with a one-dimensional scene ID will produce a high-variance estimate of the scene’s contribution to the flux. Note that the factor mapping from flux to radiance is the anisotropy factor, not the ADM. The ADM is a model for the anisotropy factor (or correction).

Line 213: This does not make sense to me. CERES flux is computed over on the order of 20 km FOVs, CERES does not measure at the scales of pixels in the LES simulations. Moreover, each CERES flux estimates a contribution to the flux at TOA from a localized region (the ~20 km FOV), the radiation from that region reaches TOA spread over a ~hundred km region. See, for example, the difference between the MISR restrictive and expansive albedos. F_3D is the flux at TOA, and so of course it is spatially smoothed as the upwelling flux at each horizontal location is sourced from a huge area on the surface, due to integration of upwelling radiance over angle.

Line 219-223: It sounds like the CERES-type flux referred to in this paper is a non-standard quantity that warrants a clear precise definition.

Line 223-224: “The ADM is the same for all cloudy pixels.” This is incorrect.

The ratio between flux and radiance (the anisotropy factor) varies everywhere in space and angle and is defined everywhere within the 3DRT domain. It is not constant over a scene or small LES domain. CERES approximates the anisotropy factor as constant over a large (order ~20 km) region. The definition for the CERES flux relationship (i.e., between a localized region in a FOV and a flux spread over the TOA) can be applied at higher spatial resolution. This is exemplified in the MISR restrictive albedo and local albedo products, the latter of which is a TOA flux product at 2.2 km resolution (though not broadband). The difficulties here are in the geometric definition of the reference levels for registering TOA flux contributions to, and the ability to produce a model for the anisotropy. This becomes increasingly difficult at high resolution (e.g., ~100 m) because there is no one-size-fits-all definition of a reference level for which we can construct useful low variance models for anisotropy. These issues are irrelevant when the cloud is specified and the albedo susceptibility can be calculated exactly using appropriate numerical modelling.

Line 733-734: Its not flux, it’s a broadband radiance. Given fixed profiles of absorbing gases (or their absence), it would be weird if broadband radiance and bi-spectral radiances weren’t highly correlated.

Line 737-740: These statements are not justified based on the evidence presented either in the paper or with appropriate references.

Line 829-831: This is unjustified, again, as 3D effects on albedo susceptibility have not actually been calculated.

Reference (Zuidema et al., 2008) and discuss.

1. Droplet Concentration

My challenge to the authors is to better explain their choice of definition for droplet concentration retrieved from bispectral retrievals, as it differs from how such retrievals are used in practice. So, for general readers to get useful information from the study, I think it would be beneficial to directly engage with this issue and address it clearly in the text.

Eq. 1: Why should anyone care about this definition of vertically-averaged Nd? As noted above this Equation in the text, the reference Nd for in situ studies is the average of Nd across the vertical extent of the cloud (or the Nd at cloud base). The vertical averaging of Nd is also the reference used for field validation of remote sensing retrievals of droplet number concentration (Gryspeerdt et al., 2022; Painemal and Zuidema, 2011). Most of the theory used in ACI analysis uses a simplified adiabatic framework in which Nd is constant with height (not accounting for expansion with height i.e., geometrically thin layers). The reasons for these definitions are simple; to isolate the effects of droplet concentrations from other effects (e.g., dynamical and thermodynamic), even if through an incomplete characterization of the 3D Nd field using assumptions that introduce errors. The isolation of droplet concentration is critical to ACI analysis. By using an Nd weighted by extinction coefficient as a reference, this utility is lost, so by choosing this reference there is no traceability to existing ACI analysis.

So, why should I worry whether retrievals agree with the extinction weighted Nd_LES, or not?

If there is a need to change the definition/interpretation of remotely-sensed droplet concentration from quasi-adiabatic to retrieving Eq. 1, then this is an important point that needs to be clearly communicated to the communities that use these retrievals. If this is the case, then I suggest making that argument be the focus of the paper.

For example, the argument might go: “Due to our inability to specify appropriate microphysical profile information, we are unable to usefully bound uncertainty in droplet concentration and therefore must restrict the definition to an extinction-weighted quantity and limit the theoretical insight that is available.”

If the authors are not taking a strong position on how droplet concentration ‘retrievals’ are interpreted, it would be useful for them to cleave to the existing definitions and thereby provide useful error characteristics for people using bispectral retrievals to infer droplet concentration. As is, the presented results have limited utility for refining the interpretation of existing studies. The same limitation holds for Kokkola et al. (2025). Gonzalez et al. (2025) take a different approach and should be discussed.

References: (Gonzalez et al., 2025; Kokkola et al., 2025) (see bottom for full citation).

Line 159: Cumulus rising into stratocumulus is rather complex microphysically. Should this cloud field be considered representative? How can the veracity of the cloud microphysical properties in the simulations be evaluated? Some further supporting evidence or commentary on this aspect should be included.

Line 288: How is the CBH and CTH defined? i.e., how do you separate between and cloudy and clear volumes in the model? I ask because the order of magnitude difference between the extinction-weighted and pure droplet concentration averages in the appendix suggest a very strict criterion for clear sky. Commonly, these definitions are designed to pursue coherence between models and in-situ measurements and are based on the sensitivity of the in-situ measurements; e.g., 0.01 g/kg or 10#/cm^3 etc. as in other studies that examine microphysical effects on susceptibility equations (Feingold et al., 2022) (This reference should be discussed in the text). I suggest that this point be examined in more detail as the order-of-magnitude differences seem larger than the errors in Eq. 3 estimated from other LES or from in-situ measurements (Feingold et al., 2022; Grosvenor et al., 2018).

Line 350-352: Nd_LES is not the reference point for adiabatic behaviour so disagreement between Nd_1D and Nd_LES are not necessarily evidence of deviations from adiabatic conditions. If the cloud is adiabatic then Nd_1D will agree with both the vertical average of the droplet concentration (no extinction weighting) and Nd_LES. However, agreement between Nd_1D and Nd_LES does not necessarily mean the cloud is adiabatic. This is just one of the complications of the chosen definition.

Several figures (e.g., Fig. 4&5) show comparisons of retrievals but not the reference (regardless of its definition). Please include the reference/truth in the figures so we can understand which errors compensate.

There are exact calculations for the partial derivatives  (whatever the definition of Nd). Regression across columns and a cloud field does not provide an exact reference because it can include unwanted covariates, e.g., a correlation between mean droplet concentration and droplet profile shape, which will bias the power-law relationship. Please compare the estimates to the exact calculation for each column.

Technical Comments.

Line 53: Perhaps remote sensing retrievals rather than instruments.

Line 59: Twomey & Seton 1980 is the earlier paper where bispectral sensitivity is introduced.

Line 70: Should “Most” operational retrievals be “All”?

Line 81: I suggest adding Zinner et al. 2010; Cornet & Davies

Line 90: Várnai and Davies (1999) did not analyse retrieval accuracy.

Line 86-93: At which wavelength are changes in cloud reflectance being used to define “brightening” and “darkening”. Changes in the relative amount of brightening and darkening across visible and absorbing wavelengths affects retrieval errors.

Line 93-99: I’m not sure what the message is. With the “Although XXX, previous studies have shown YYY” construction, is it saying that out of the several factors (variability in cloud top height, solar and view geometry, and photons leaking from optically thick to optically thin cloudy regions) that only solar-viewing geometry is significant? I suggest changing “photons leaking …” to “light scattering from optically thick to optically thin regions”.

Line 111: Gryspeerdt et al. 2019 and associated sentence does not seem to mix with the rest of the paragraph, which are about retrieval errors, not ACI in general.

Line 167: What is the range of the droplet size bins?

Line 196: Does this mean there is integration of multiple monochromatic reflectances over the band? Averaging of optical properties over the band? Or just a single monochromatic calculation at each nominal wavelength.

Line 191-205: What is the domain top of the RT calculations? Is it the LES top of 3 km? or based on a particular atmospheric profile?

Line 315-316: No need to cite Loveridge & Di Girolamo (2024) here as that study just employs simplified versions of microphysics based on other studies.

Line 531-532: Aren’t PPHA biases caused by sub-pixel heterogeneity?

Line 533-534: It shouldn’t be regardless. There should be logic motivating the analysis that shouldn’t be waved aside.

Line 547: And plane-parallel optical depth bias contribution?

Line 839-840: Sinclair et al. 2019 does not use active instruments.

Fig. 6&7: The dashed and solid lines for the PDF and the mean do not correspond to each other in the legend, which is confusing.

References

Doicu, A. and Efremenko, D. S.: Linearizations of the Spherical Harmonic Discrete Ordinate Method (SHDOM), Atmosphere, 10, 292, https://doi.org/10.3390/atmos10060292, 2019.

Feingold, G., Goren, T., and Yamaguchi, T.: Quantifying albedo susceptibility biases in shallow clouds, Atmospheric Chemistry and Physics, 22, 3303–3319, https://doi.org/10.5194/acp-22-3303-2022, 2022.

Gonzalez, J., Dipu, S., Jimenez, G., Camps-Valls, G., and Quaas, J.: Machine Learning-Based Retrieval of Cloud Droplet Number Concentration and Liquid Water Path From Satellite Spectral Data, IEEE Journal of Selected Topics in Applied Earth Observations and Remote Sensing, 18, 21910–21922, https://doi.org/10.1109/JSTARS.2025.3601981, 2025.

Gryspeerdt, E., McCoy, D. T., Crosbie, E., Moore, R. H., Nott, G. J., Painemal, D., Small-Griswold, J., Sorooshian, A., and Ziemba, L.: The impact of sampling strategy on the cloud droplet number concentration estimated from satellite data, Atmospheric Measurement Techniques, 15, 3875–3892, https://doi.org/10.5194/amt-15-3875-2022, 2022.

Painemal, D. and Zuidema, P.: Assessment of MODIS cloud effective radius and optical thickness retrievals over the Southeast Pacific with VOCALS-REx in situ measurements, Journal of Geophysical Research: Atmospheres, 116, https://doi.org/10.1029/2011JD016155, 2011.

Grosvenor, D. P., Sourdeval, O., Zuidema, P., Ackerman, A., Alexandrov, M. D., Bennartz, R., Boers, R., Cairns, B., Chiu, J. C., Christensen, M., Deneke, H., Diamond, M., Feingold, G., Fridlind, A., Hünerbein, A., Knist, C., Kollias, P., Marshak, A., McCoy, D. T., Merk, D., Painemal, D., Rausch, J., Rosenfeld, D., Russchenberg, H., Seifert, P., Sinclair, K., Stier, P., van Diedenhoven, B., Wendisch, M., Werner, F., Wood, R., Zhang, Z., and Quaas, J.: Remote Sensing of Droplet Number Concentration in Warm Clouds: A Review of the Current State of Knowledge and Perspectives, Reviews of Geophysics, 56, 409–453, https://doi.org/10.1029/2017RG000593, 2018.

Kokkola, H., Tonttila, J., Calderón, S. M., Romakkaniemi, S., Lipponen, A., Peräkorpi, A., Mielonen, T., Gryspeerdt, E., Virtanen, T. H., Kolmonen, P., and Arola, A.: Model analysis of biases in the satellite-diagnosed aerosol effect on the cloud liquid water path, Atmospheric Chemistry and Physics, 25, 1533–1543, https://doi.org/10.5194/acp-25-1533-2025, 2025.

Zuidema, P., Xue, H., and Feingold, G.: Shortwave Radiative Impacts from Aerosol Effects on Marine Shallow Cumuli, Journal of the Atmospheric Sciences, 65, 1979–1990, https://doi.org/10.1175/2007JAS2447.1, 2008.

Review of "Impacts of the Three-dimensional Radiative Effects on Cloud Droplet Number Concentration Retrieval and Aerosol Cloud Interaction Analysis"

by Ademakinwa et al.



The manuscript adds some useful analysis  to the already published state of knowledge of 3D radiative transfer and inhomogeneity effects influencing passive satellite retrievals. The authors do not simply repeat earlier studies of 3D effects on cloud property retrievals, but follow the impact on retrievals of droplet number concentration Nd from synthetic cloud model truth to far reaching conclusions based on such satellite retrievals on aerosol-cloud effects in other publications (Twomey effect and the connected cloud albedo susceptability). Although the approach is not new (LES model as basis of synthetic measurements), demonstration of the effect leads to some clear conclusions, I have not seen summed up so nicely anywhere else before.



The paper is largely well written. At some places I see potential for some tightening of the text and removal of uneccessary detail.



I suggest publication after minor revision.  



--- Whenever I ask for clarification or explanation in the following, I usually ask for it to be included in the manuscript, not in an answer to the reviewer. ---



General points:



1. Underestimation/Overestimation: You use this term to compare 3D RT based results vs 1D RT based results. That does not sound right. To my feeling these comparative terms are used to compare to the truth - which you almost nowhere do. In addition, if you use them for 3D vs 1D, 3D is definitely closer to beeing "truth". Example: "3D RT based underestimate 1D RT based" sounds awkward. It rather is "1D based overestimates 3D based" or "3D based is larger than 1D based".

E.g. l.508/509, l.730, l.783, l.797, ...



2. Connected to point 1. At several points I'm missing the comparison to the "truth". Do you not show it on purpose?  

E.g.  l.551+556, Fig.6+7 - Why not show Nd_LES PDF here?

l.562-571 - Whether retrievals are better or worse can not be checked as you do not show the true Nd.



Details:



l.31 - "plane-parallel effects": Only 3D experts know what you're talking about. Rather use "averaging effects" or "the use of the plane-parallel averaging assumption".



l.33-35 - Please already mention here why this is true - "if albedo-Nd sensitivity is derived in a radiatively consistent way".



l.121 - "few have": Please add or repeat citations of papers who have.



l.210 - Acronym I3RC has not been introduced.  



l.212 - The "CERES algorithm" needs a citation or extra explanation please.



l.237 - Please give reference to the original publications on such retrievals by Nakajima and King (1990) and Platnick et al (2003) showing the facts you refer to here.



l.300 - What is the fixed fraction f_ad? Is it one number? Can you give it here?



l.304 - Brenguier et al.(2000) or even earlier authors already set up the adiabatic cloud model. Grosvenor nicely summarized it. Please mention the more original publication too.



l.339, section 3.1: This a 1D RT experiment here, excluding all 3D RT. Please, clarify early. I needed a while to get it.  



l.344: Do you see a way to simplify your notation of e.g. "Nd_cal^1D(lambda_abs)". Isn't it enough to have the litte "1D" and "3D" in the superscript as soon as it is RT based (skip "cal")?  

l.355, Fig.2, "1D RT bi-spectral retrievals" - This is not the most precise wording, is it? Each retrieval in this manuscript is "1D" or "1D RT based", because it doesn't use an 3D RT inversion or correction. It should rather read "retrievals based on 1D RT tabulated reflectance". Please clarify wording throughout the manuscript for these cases. It can be quite confusing in the beginning otherwise.  

(similar e.g. in l.613 or l.634/635)



l.375 - Please give a summary sentence on the VW method by Miller et al.



l.380 - I don't understand the motivation behind the no drizzle test. It can be assumed that the drizzle drops > 30mu don't have a large impact on radiation (small numbers tail of the size distribution, large forward scatter) most of the time. However,  if there would be many droplets>30mu they will have radiative impact and you would need to consider them, wouldn't you?

Anyway, the figure shows that this test is not relevant too. I would suggest to only mention your result (and state "not shown"). I would also remove them from Fig. 3 where the difference is hardly visible.



l.386 - I do see three Nd PDF derived from LES "cal" and three retrieved at different channels, but no further "derived from retrievals under the different levels of constraints". Please clarify.



l.395, Fig.3 - Here the sub and superscripts get too small and unreadable. Please improve.



l.454 - You cannot expect that re(VW) as an average provides a better agreement than the cloud top leaning re*, if your Nd calculation assumes a cloud top value, can you? Please clarify.



l.467 - What is "almost similar"? Sounds like "very different".



l.470 - Are peaks smaller in frequency? Or in Nd?

l.467-477 - Please consider shortening here. Wording is rather un-precise. And I'm missing the rough reasons (3D reflectance smaller due to "channeling" or "diffusion" from large to small optical thickness, leading to smaller tau and larger re, leading  to smaller Nd).



l.475 - I would not call these "narrow peaks". To me this is a misconception of the lower boundary value "0". You should also cut the x axis at Nd=0 cm-3 and not at Nd=-5 cm-3 in Figs. 4, 6, 7.



l.512-517 - Please check. It's either my confusion or you're mixing up things here. Differences between spectral bands are driven by absorption differences, yes. But 3D effects are not. The effect that leads to darkening for high sun is enhanced (macrophysical) forward scatter from exposed tops and regions of large optical thickness due to cloud geometry (downward "channeling"). It is not enhanced absorption. The same enhanced macrophysical forward scattering leads to average brightening for low sun.



l.531. Acronym PPHA never defined.



l.573, Fig.8 and l.581-588 - This might be information you could summarize and say "(not shown)".  



l.590, section 3.4 - Why don't you show the real Twomey effect in this section - the truth? LWP from LES, Nd_LES and R_BB from 3D RT?



l.615, Tab.1 - Please comment on the awkward threshold values. How did you find them?



l.664 - Please check equation. It does not seem correct unit-wise.



l.666 - An "alpha" instead of an "alb".



l.678 - Please remove the binning from the Fig. caption.



l.691 - Fig. 10+11, It would be nice to relate Fig 10 and Fig 11 by showing S_alb,rel values (and according line fits through R_BB and N ?) in Fig 10. Then the reader could compare the SZA=50 result to results over all SZA in Fig 11.

Second point - Why not use colored lines here on top of using symbols? You used a lot of color in all other plots.



l.725 - I don't see a "more pronounced decrease at larger LWP" above 100.  



l737 - "concerns about 3D effects" - Isn't it the 3D effects which (do not) impact and not the "concerns about"?



l745 - You put the importance of Nd accuracy first here, but I'm missing the clear conclusions on a "best-practice" here.



l.767, "reference LES Nd" - Why not stick to "Nd_LES"?



l.789-799 - I think a more compact summary and conclusions would be nice after a complex manuscript. Here, e.g., I would avoid to start talking about PDF distributions again.



l.800-810 - Why not generalize the conclusion for all absorbing channels? Above you stated that there is no difference.



l.842 - I'm not sure that you need the appendix. I would prefer a simple statement in the main text with something like: "Column averaging is not useful. Optically irrelevant, i.e., optically thin parts at cloud edges would dominate averages or make arbitrary cut-offs of small LWC necessary".