The manuscript leverages on existing CMIP6 simulations, in particular doubled dust experiments within AerChemMIP, to infer model impacts of dust on the Asian Summer Monsoon, using 7 pairs of simulations with different models in atmospheric only configuration. Relations among simulated variables from the multi-model mean and (in most cases) individual models are shown and discussed to provide a coherent picture of possible underlying mechanisms of observed dust perturbations to the system. I found the manuscript interesting and generally well written. I do have, nonetheless, a couple of general remarks and a few specific comments.

Starting from the title there is some emphasis on “atmospheric absorption”. However, if space is dedicated to the consequences, I found little details on its causes, both in terms of discussing the possible mechanisms, and in terms of displayed variables. In particular, it is not very clear which modeled processes are being actually simulated (SW-LW interactions, CCN/IN) and not enough details are provided in terms of shown variables (e.g. only net ERF is shown for individual models; dust-cloud interactions are deemed insignificant but not shown). I would suggest discussing a bit more in detail possible mechanisms at least in the introduction, and be more thorough in reporting the relevant available variables.

There is also, here and there, some lack of attention for details (plots in the supplement slightly different than the corresponding versions in the main text, missing references, imprecision in reporting models’ relevant features, …) that warrants an accurate revision.

Specific comments

38 > What do you mean by “most of these mechanisms are model-based”? Please rephrase

86-88 > This sentence seems a bit contradictory: if emissions data files could be scaled, that could imply that dust emissions are prescribed. So why do you state that all models calculate dust emissions online? Please be more specific about the different strategies of the simulations involved in this study, if known, otherwise comment on that.

91-92 & Table 1> In this context, we are not really interested in whether dust-cloud interactions could be turned on in a model, but rather if they were actually activated in these simulations. By the way, I would strongly suggest reviewing all the information reported in the table. For instance, the IPSL model version used in CMIP6 does not have dust-cloud interactions of any kind, and the reference provided describes a post-CMIP6 version of the model, with 4 dust modes – not one. There may be analogous imprecision concerning other models. Please double-check everything carefully.

98 > What kind of interpolation did you use? Bi-linear?

109-110 > “regions where there are inconsistent responses across models, defined as regions where ≤4 of the 7 models have the same sign as the MMM”. This definition is clearly stated, and in most cases individual model results are available in the supplement and differences discussed in the main text. However, often in the text expressions like “most models” (e.g. line 172) indicate a 50% + 1 situation, rather than a clear majority. This highlights the inherent difficulties of this exercise. Maybe add some comments about this in the text.

126 > “hatches in (f) denote statistical insignificance at the 10% level”. This phrasing is a bit confusing, considering what we see in the plot. Please adjust/rephrase. In addition, here and everywhere else in the captions of figures in the main text and supplement, clarify the metric used, e.g. using a two-tailed student’s t test …

133-134 > The MMM represented in both Figure 2b and Figure S6h shows differences at least in the hatching. If a different criterion and/or subsets of simulations were used in the submitted version of the manuscript, compared to what was initially tested for this work, please revise and make sure figures are consistent - this applies to many of the plots. In fact (minor) differences in plotted variables values (considering obvious cases where color scales match) and/or hatching also appear in Fig. 2a vs S5h, Fig. 2c vs S7h, Fig. 6a vs Fig. S11h, Fig. 6c vs S12h.

135-136 > I would add something like “although not necessarily statistically significant”

147 > It would be interesting to see also the individual models SW vs LW partitioning, as done for all other variables.

150 > The notation “Ocean” is rather misleading, considering that the Arabian Sea and portions of the Indian Ocean show the opposite situation. I would suggest using again “Tropical Western Pacific Ocean”.

152-155 > “robust common patterns” seems too strong a statement, compared to what we actually see. Also “All models show that such changes come from … changes in mid-level clouds (700-200 hPa) above the Chinese deserts (Figure 3b)” is inconsistent with at least two models showing the opposite. Please re-write this paragraph accounting for the actual variability emerging from the figures. More in general, try to be more precise when discussing the variability among individual models, and otherwise specify when you are discussing the ensemble mean specifically. This is done in some passages, but not systematically.

156-157 > All statements about dust-cloud interactions seem highly speculative, unless we see specific diagnostics (for the subset of models actually parameterizing this process in the simulations at hand). There is also the potential contribution of semi-direct effects, which is not mentioned.

163 > It is not clear what you mean by “hemispheric asymmetry”. Since you were just discussing the Indian subcontinent (and later on you add the Arabian Peninsula etc.) versus the “Tropical Western Pacific Ocean”, one would imagine that you are implying a zonal asymmetry. Please clarify. 

169 > “in response to INCREASED dust emissions”

173-175 > I would leave out the Arabian Peninsula, as it does not fit the given description of what happens in the listed models. It is also not clear to which regions in particular the definitions of Central and East Asia apply. In fact, these two sentences are overall quite unclear / imprecise in describing the corresponding plots. Please clarify.

184-186 > This may hold for India, but not for instance for the Arabian Peninsula. Hard to generalize.

210-211 > Is climatology from the MMM?

238-239 > (Maharana et al., 2019; Bercos-Hickey et al., 2020; Cruz et al., 2021; Lau et al., 2006). These references are not in the bibliography. (Balkanski et al., 2021) could be a relevant reference in terms of mechanism, however it is not pertinent considering the way the paragraph is currently phrased, i.e. it does not focus on the ISM, but on the West African Monsoon; please rephrase.

262-263 > I fail to clearly see this hemispheric asymmetry from the results presented in this study. (Evans, 2020) is also missing from the reference list

289-290 > Same as above

330-331 > It may be worth showing

Review of “The key role of atmospheric absorption in the Asian Summer Monsoon response to dust emissions in CMIP6 models” by Zhao et al.

Summary

This study investigates the response of the Asian Summer Monsoon (ASM) to a doubling of dust emission in a subset of Coupled Model Intercomparison Project Phase 6 (CMIP6) models. The manuscript describes differences in dust effective forcing (net flux differences between 1x and 2x dust emission) and the resultant changes summertime atmospheric moisture and regional circulation. The main findings of this study are that the doubling of dust results in atmospheric heating over the continent that, via the resultant hemispheric energy imbalance and circulation response to that imbalance, enhances the monsoon over the Indian subcontinent. There was no strong model consensus regarding the effect of the doubling of dust emission on the East Asian Monsoon (which I suggest could imply that there is not a strong one).

The topic of how dust emission affects monsoonal precipitation is interesting and the CMIP6 data set is a novel one to use for the analysis. My critique of this manuscript is that it mainly describes discrepancies in the models’ response to the dust radiative forcing, rather than providing any insight into the causes of those discrepancies, where the latter would make for a more interesting and potentially useful study. The authors imply that it is not possible to understand the source of the model discrepancies because the requisite data is not available (Lines 313-315). However, I think a little digging into the models’ representation of dust could at the very least tell us something about the prescribed dust optical properties, which the authors indicate as being fundamental to the forced response. The authors could even diagnose which models have larger dust absorptivity by examining the differences (differences between the 1x and 2x dust emission) in SW atmospheric net fluxes. After reading the manuscript I’m left with the impression that the authors feel like it’s just not worth trying to understand the sources of the model discrepancies.

Specific Comments:

1. Abstract: “Our results demonstrate the central role of dust absorption in influencing the ASM”. I understand that this is implied by the analysis. However, isn’t it possible to identify which models exhibit the strongest (presumably) solar absorption by dust and then demonstrate that the magnitude of the effects on the ASM are somehow correlated to that absorptivity?
2. Line 20: I don’t think the Kok 2018 reference is appropriate here.
3. Line 34: Extra “)”
4. Line 50: “found” is redundant.
5. Line 136: Should be Fig 2b
6. Line 145: Should this be “a doubling of dust emission”?
7. 2a & b: Why is there more inter-model agreement in the all-sky ERF than in the clear-sky ERF over the Indian subcontinent? If the model differences in clouds are forced by the changes in the dust ERF, I’d expect more uncertainty in the all-sky ERF than in the clear-sky.
8. Line 164: The hemispheric asymmetry in dust radiative forcing has been documented and examined by other studies, and I think it would be reasonable to cite those here.
9. Lines 172--178: throughout this manuscript, I think the authors are missing an opportunity to provide insights into the causes of the discrepancies among the modeling, and here is one such example. The authors describe the differences in the modeled responses to the doubling of emission over Asia land surfaces. They note that four models show warning temperatures, while the others show cooling. The authors go on to point out that these models’ mean states have the least amount of emission, and consequently the smallest increase in dust optical depth for the experiment. My suggestion is that the authors propose and test a hypothesis explaining why there may be a connection between the apparent over-land warming and small change in the absolute dust emission. This would be far more interesting and insightful than just describing the differences between models.
10. Lines 184—186: Please be clear if you are discussing the clear-sky or all-sky ERF. It would be nice to not have to reference the figures to obtain this information.
11. Line 186: I don’t understand what is meant by “the central role of dust-radiation interactions in changing the surface radiation budget and temperature”. Are the authors suggesting that the surface energy budget over Asia is, to first order, controlled by dust? I doubt this is the case since it’s a rather extreme claim, and suggest that the text be revised to be more precise/clear.
12. Line 249: The statement “The East Asian Summer Monsoon (EASM) presents a mixed response (Figure 6d) to dust emissions” is a little strange to me since it implies that the models are telling us something concrete about the effect of dust radiative forcing on the monsoons, yet in the paper the authors are telling us that the models are all over the place and so we shouldn’t trust them.
13. Line 314: The authors state that modeling centers should provide more information on dust single scatter properties and size distributions. However, I’m sure that these data are, to some extent, available in the mode descriptions. I wonder if the authors could do a more thorough job of diagnosing the underlying causes of inter-model discrepancies by comparing, for example, differences in dust single scatter albedo, since this would play a very large role in determining net radiative forcing.
14. I was surprised that the authors didn’t examine the cloud radiative effect in the experiments, since changes in cloudiness play such a strong role in the response. This could be a useful metric.
15. With regards to diagnosing temperature changes, I suspect that an energy budget analysis would allow the authors to make a stronger and quantitative case for the relevant factors shaping the differences in temperatures between the experiments.