Review is attached in pdf.

This article presents a comprehensive analysis of the effect on climate of specifying dust mineralogy in the GFDL AM4.0 model. This is a topic of great current interest with the success of the Earth Surface Mineral Dust Source (EMIT) mission. Overall the paper is well written and presents interesting and topical results. I have a few important concerns but am hopeful that the paper will be suitable for acceptance after major revisions.

My main concern is with the framing of the results. Specifically, the authors mostly compare the HD27 run with three mineralogy-resolved runs with different mixing rules (VOL, MG, and BM). The problem is that not one but two important things differ between HD27 and these three runs: (1) the mineralogy is resolved only for the VOL, MG, and BM runs and not for HD27, and (2) the absorption in the mineralogy-resolved runs is only about a third of that in HD27, which is clearly too absorbing in comparison to AERONET (Fig. 3) and other data. So the large differences in radiative fluxes (Figs. 4-6, 8), temperature (Fig. 10), soil moisture (Fig. 11), wind (Fig. 12), and precipitation (Fig. 13) between HD27 and the mineralogy-resolved runs are predominantly because of the very large difference in atmospheric absorption between these runs, whereas mineralogy being resolved or not plays only a minor role. The authors acknowledge this in various places (e.g., Fig. 7) but still commonly present their results as being due to resolving mineralogy, which I think is not accurate and misleading to the reader. Examples include:

• Line 21 – 23 (abstract): “Resolving dust mineralogy reduces dust absorption and results in improved agreement with observation-based single scattering albedo (SSA), radiative fluxes from CERES (the Clouds and the Earth’s Radiant Energy System), and land surface temperature from CRU (Climatic Research Unit), compared to the baseline bulk dust model version.” But these improvements are driven predominantly by reducing dust absorption (i.e., this happens in going from HD27 to HD09), which is set to an unrealistically high value in the control run, to a more reasonable value, irrespective of whether or not the mineralogy is resolved.
• Line 25-26 (abstract): “[Resolving dust mineralogy] leads to a reduction of over 50% in net downward radiation across the Sahara and approximately 20% over the Sahel at top of atmosphere (TOA).” This again is primarily due to the reduction in dust absorption, not because of resolving dust mineralogy.
• Line 437-9: “resolving mineralogy turns out to induce substantial decrease in NET flux at TOA, with a more than 50% negative anomaly over the Sahara and around a 20% negative anomaly over the Sahel (see values in parentheses in Figure 4 i-l).” Here again the attribution to resolving mineralogy seems inaccurate. The authors obtain similar results simply by scaling down the unrealistically high absorption in HD27 to a more reasonable value (in HD09). The authors note this in the next sentence but still leaves the reader with the impression that this is due to resolving mineralogy.

The key issue in all these examples (and various other ones throughout the paper) is that the authors present the reduction in dust absorption as being a result of resolving dust mineralogy, but this is artificial because the absorption was set to a very high value and we’ve known for a while know that absorption is much lower than used in the HD27 run (e.g., Balkanski et al. ACP, 2007; Di Biagio et al., ACP, 2019; Adebiyi et al., Comm Earth & Env, 2023).

To address this, I recommend that the authors first have a section where they analyze the effects of dust absorption by comparing HD27 with HD09 – since HD09 has more realistic absorption that is similar to that in the mineralogy-resolved runs - and only then analyze the effects of resolving dust mineralogy by comparing HD09 with the three mineralogy-resolved runs. This would separate the effects of reducing absorption to a more realistic value from the actual effect of resolving mineralogy, thereby preventing the reader from misunderstanding the attribution of the results, and would get the paper’s main points across more clearly and accurately.

Relatedly, I think figures 4-6 should be removed because the differences in fluxes here are primarily because of the very large difference in absorption between HD27 and the mineralogy-resolved cases, not because of resolving mineralogy per se. So these figures can cause readers to draw the incorrect conclusion that these flux differences are due to resolving mineralogy. Instead, the authors could show figures comparing HD27 to HD09 (i.e., expand the current Figure 7 into three figures similar to Figures 4-6).

Another concern is that the authors assess the effect of mineralogy on absorption and SSA using comparisons against data, but do not sufficiently consider the effect of particle size in these comparisons.

• For instance, on line 346 they state that the high standard deviation of SSA in AERONET data is due to spatial variability in mineralogy but this could also be due to spatial variability in the dust size distribution. As far as I can tell, the authors are not able to distinguish between those two sources of SSA variability in the real world.
• Similarly, line 361 states “The underestimation of regional SSA contrast in AM4.0 suggests the need for a higher regional contrast in iron oxides content”. But a higher regional contrast in the dust size distribution would similarly increase variability in SSA.

More clearly addressing the effect of model errors in the size distribution is important since the size distribution affects most/all of the results presented in the paper and because it seems that (super) coarse dust accounts for a lot of the absorption over North Africa (e.g., Ryder et al., ACP, 2019, Figure 7c) and it’s unclear to what extent this is represented in the current paper.

To address this, I recommend that the authors are (1) clearer about the exact size distribution they use in their simulations (see comment below) and (2) discuss clearly that errors in both size distribution and mineralogy can cause the disagreements against the SSA AERONET data.

My final major more substantial comment is that I find it difficult to pinpoint exactly what we have learned from this paper that we didn’t already know from previous studies of the effect of dust absorption on radiative fluxes and the monsoon over Northern Africa (e.g., Balkanski et al., ACP, 2021) and the effect of resolving mineralogy (e.g., Scanza et al., 2015; Perlwitz et al., 2015; Li et al., 2021; Li et al., 2021; Gonçalves Ageitos et al., 2023; Obiso et al., 2023). I would suggest spelling this out more clearly in (especially) your conclusions section.

Other comments:

• There is some confusing wording in the paper when it comes to describing the differences between the different runs, which is often the difference in the difference between radiation calls with and without dust. For instance, I think line 25 (Abstract) should read “it leads to a reduction of over 50% in the dust effect on net downward radiation” (underlined words were added). There are similar issues with wording in the conclusions section (e.g., lines 728-730)
• In section 2.1, what are the exact size ranges of the bins? And what is the choice of the emitted fraction per bin based on?
• Line 139-141: Could you specify which algorithm you are referring to here, exactly? Is this from previous work? If so, please provide a reference.
• Line 154-6: This 5% seems arbitrary. Could you elaborate on how you chose this? What is the sensitivity of your results to this external mixing threshold?
• Line 167-170: More details here would benefit the reader and make it easier to appreciate your results. Could you give a basic description of the Maxwell-Garnett and Bruggeman mixing rules and explain the difference in the resulting optical properties?
• Section 2.3 and 2.4: why use AERONET and laboratory SSA, but not satellite data and in situ measurements?
• Table 2: which mixing rule was used for HD09 and HD27?
• Line 252-3: What data are you using for the t-test? Would this be the result of the 19 individual years in each run? Please elaborate.
• Figure 1: The imaginary index of refraction here makes no sense to me here. This should decrease with wavelength in the SW spectrum for hematite, HD09, and HD27 as dust is well-known to be more absorbing in blue and UV than red (e.g., Di Biagio et al., ACP, 2019). Is there a mistake in this plot? Also, the dotted line should be defined in the caption and the black and gray lines are invisible in panel a.
• Line 270: I think “solar spectrum” here should be “visible band” instead, based on the caption to Table 3. Also, please indicate the effect of averaging over the visible band, so your results can be compared with those of other studies, which usually report AOD at 500 or 550 nm.
• Table 3 should include more recent comparisons than with Huneeus ’11, which is getting pretty old, such as from CMIP5 (Wu, Lin & Liu, ACP, 2020), CMIP6 (Zhao, Ryder & Wilcox, ACP, 2022), DustCOMM (Kok et al., ACP, 2021), AeroCom3 (Gliss et al., ACP, 2021), etc
• Line 337 onward: Please clarify how exactly you calculate the standard deviation on SSA. Is this only for model values at the AERONET stations in Figure 2?
• Line 337 onward: Please include a plot (in the supplement or the main text) of the SSA standard deviation versus SSA showing the various experiments and the AERONET data to inform the discussion here.
• Line 359: I think it’s worth emphasizing here that the dynamic range of SSA is greatly underestimated (model variability in SSA is several times smaller than seen in the real world!), even after accounting for mineralogy. There’s clearly something important still missing.
• Line 435: please state here or elsewhere whether your model accounts for LW scattering or just LW absorption.
• Table 4: please clarify what the standard deviation represents. Is this the standard deviation over the 19 simulation years?
• Line 593-6 and Section 5.3: for the benefit of the reader, please discuss here the dynamically situation that causes absorption in this instance to increase ascent and precip rather than increase stability and decrease precip, as it does in many other situations and globally (e.g., Samset et al., Comm. Earth & Env., 2022)
• Figure 13: it seems odd to me here to calculate the domain average only for the statistically significant anomalies because (1) then the anomalies mean something different for b versus d and (2) the numbers depend on only very few grid points or none at all for the Sahara in panel d, it seems, which probably should not list any anomaly then since it’s undefined.
• Lines 733-735: here and elsewhere in the paper, it would be useful to the reader if you compare your results of the effects of dust absorption on precip in the Sahara and Sahel to those in Balkanski et al. (ACP, 2021).