In this manuscript, the authors propose a method for decomposing aerosol components using particle depolarization ratios measured from lidar at two different wavelengths. The methodology is presented in detail for cases involving mixtures of two and three aerosol components, respectively. Case studies are conducted for mineral dust from Arabian, Asian, and Saharan sources. The method is comprehensively described, and the case studies provide a thorough experimental validation. Given the increasing availability of multi-wavelength lidar measurements, this work represents a valuable contribution to the lidar and aerosol observation communities. However, I have one major comment regarding the methodological analysis, along with several technical and minor comments. Additionally, the manuscript would benefit from proofreading by a native English speaker to improve clarity and flow.

Major comment:

The proposed method, e.g. for the mixture of two components (Eqs. 5 - 9), relies on input parameters from Table 1. These parameters undoubtedly influence the results of the aerosol decomposition, and therefore, a more comprehensive sensitivity analysis that what it has for now is needed. In Section 2.3 and Table 2, the authors conduct an uncertainty analysis for three cases with different depolarization ratios at 355 and 532 nm, comparing reference results with those obtained using Monte Carlo simulations with normal distributions for all input variables. However, the analysis does not address the sensitivity of the results to individual variables. Specifically, which variables have the most significant impact on the decomposition results? For instance, the Ångström exponent is known to vary considerably from different studies, but its specific influence on the results presented in this manuscript remains unclear. While I acknowledge the authors’ point that this paper primarily aims to present a method rather than investigate aerosol characteristics (which is beyond the scope of this work), understanding the sensitivity of the results to the input parameters is crucial. Such an analysis would help identify which parameters require more careful consideration in future applications. Furthermore, a sensitivity study could provide a statistical explanation for why certain points in Figure 5 deviate from the curve.

Other comments:

The abstract of this manuscript needs to be improved. Lines 4 - 6: The authors state the advantages of the proposed method, but the logic may confuse readers. Specifically, “And it requires the proper knowledge of characteristic depolarization ratio and the backscatter-related Ångström exponent of each aerosol type” is a prerequisite for the method, not an advantage. Please rephrase these sentences to clarify the distinction between prerequisites and advantages.

Line 12: The claim that the method is “more accurate than the common use of the ratio of the particle linear depolarization ratios” requires statistical support. Please provide evidence or references to substantiate this statement.

Line 35: The sentence is unclear and should be rephrased for better readability.

Line 63: The description of Eqs. 1-2 is confusing. The statement, “the calculation involves the aerosol backscatter coefficient (βx) and aerosol-type-specific characteristic depolarization ratio (δx),” implies that βx is not aerosol-type-specific, but I understand βx is also aerosol-type-specific.

Line 74: The “Methodology” section requires improvement. The authors list several equations (Eqs. 1-4) but do not systematically introduce the proposed method or explain how these parameters are used to develop the algorithm. The statement, “To apply the novel algorithm for the decomposition of two or three aerosol components,” is premature, as the algorithm has not yet been clearly defined. Readers must read the entire manuscript to understand how the parameters are used for aerosol separation. The authors should explicitly introduce the algorithm before discussing its application.

Line 119: The statement, “Assuming the same lidar ratios at 355 and 532 nm, these values can be used for the Åβ(355,532),” requires clarification. Please briefly introduce the lidar ratio, and also provide references supporting the assumption that lidar ratios are the same (or very close) at 355 nm and 532 nm.

Minor comments:

Line 38: Specify “the 532 nm and 355 nm wavelengths” by adding, for example, “of lidar instruments.”

Line 46: Replace “at 532 or 355 nm” with “at 532 and 355 nm”.

Line 207: “idea” -> “ideal”?

The article by Xiaoxia Shang and co-authors describes a new algorithm that allows combining several optical parameters observed by lidar at two wavelengths, to decompose an external mixture of three aerosol types, quantitavely. This new method builds on pre-existing methodologies using a single wavelength to separately quantify two aerosol types. The method assumes prior knowledge of a number of intensive optical properties: the depolarisation ratio of the three pure aerosols at each wavelength, as well as their backscatter Angstrom exponent (Table 1). A system of linear and quadratic equations is derived, which can be resolved in terms of the backscatter fraction of each of the three aerosol components. The equations define the region of the observational space that can be meaningfully populated, and the observational data do confirm the accuracy of this prediction (Figure 5). The method is successfully demonstrated for a number of aerosol mixtures, observed with differing lidar systems, in the context of dust aerosols from the Arabian Peninsula, Asia and the Sahara, mixed with other aerosols. A succinct error analysis is also included.

I definitely think that the method proposed is promising and that this article is worth publishing. I however also feel that the paper can be substantially improved with a little more in-depth analysis of some points: better mathematical analysis of the system of equations, better quantification of the observational bias and uncertainty requirements, better use of the data collected for an update of the assumptions of Table 1, better highlight of a side scientific result as explained below, and stronger conclusions. The abstract needs moreover more work to make it self-understandable. With a little additional work, I believe that the paper will become a highly-cited reference paper for a wide number of applications.

MAJOR POINTS:

1. The second half of the abstract is a little hard to follow. My suggestion is as follows (from line 6): “The mathematical relationship between particle linear depolarization ratios at two wavelengths for a mixture of aerosol components has been derived and expressed as a system of equations. The equations define the region of the observational space that can be meaningfully populated and its boundaries: the latter are determined by the depolarization ratios of the pure aerosol components, and their backscatter-related Ångström exponents. Data collected in the Arabian Peninsula confirmed the predicted region of the observational space, and resolving the system of equations allowed us to quantify the contribution of each aerosol component. The novel algorithm has been applied to synthetic dust mixtures and to actual lidar observations of Arabian dust, Asian dust, and Saharan dust, so as to decompose coarse-mode dust, fine-mode dust, and low-depolarising non-dust. The impact of uncertainties in the prior optical properties of the pure-aerosol components are discussed, together with impact of observational uncertainties and biases. The method that we propose offers a promising role of dual-wavelength depolarisation measurements for the understanding the vertical distribution of fine and coarse dust.”
2. I have not done a full analysis of the system of equations proposed by the authors, but I am not persuaded by their statement that there is always a unique solution (lines 163 and 184). What I see is a system of 6 equations and 4 unknowns (two aerosols) or 7 equations and 6 unknowns (three aerosols). One equation (sum of phis for lambda1) has been omitted and should also be included. Moreover, equation 10 is not independent of equations 5-9, so I don’t see how it can reduce the number of constrains. In other words, I think that a full mathematical analysis of the existence and unicity of the solution should be added in the paper. It is possible that the statement that “there is always a unique solution” will be found to be correct, but in the current version this is not explained or demonstrated.
3. The text on the observational uncertainties (lines 223-231) can definitely benefit from an expanded discussion aiming at quantifying observational requirements. Readers will need to know what observational accuracy they need to achieve so as to be able to apply the method proposed by the authors. I would start from what are the average and best measurement uncertainties on delta_p in the literature and finding how they impact the retrieval of the three components. I would then suggest to exploit the equations developed in the article to assess and quantify what are the maximum bias and uncertainty that can be tolerated for depolarisation measurements, when applying the method (this could be more useful than the generic statement that a “small uncertainty” is necessary (line 331).
4. When the authors encounter conditions that challenge the assumptions from Table 1, such as on lines 245-246 or line 282, I suggest to try sing the values suggested by the data themselves as a-priori, to see if there can be an improvement. I would not agree that the algorithm becomes unsuitable (line 282): it is more a case of improving the inputs, and the data collected do contain the information to do this. Also, the generic statement about the effect of averaging (lines 246-248) could be substantiated with verifying how things really are with and without the averaging (either using the original measured data, or if these are not available anymore, with a simulation).
5. Figure 5 shows a very interesting scientific result which it may be worth discussing in the article better, although it isn’t the main focus of the article itself: for this dataset, the figure shows that dust with a higher centre of mass altitude is coarse (mixed with non-dust) and dust with a lower centre of mass is fine. True that something along these lines is later discussed with Figure 6, but I would say that it is Figure 5 that shows this result at best and it is worth highlighting (and repeat in the conclusions).
6. The conclusions as formulated are rather weak: they are mainly a summary of the article with only the last 10 lines discussing some connections with the existing literature. These conclusions should be strengthened: I believe that the method proposed could have a sensible impact on future research, therefore this could be discussed. Some points to consider for discussion in the conclusions:
   • Potential atmospheric situations where the method could bring an advantage (this is in part attempted in the current version)
   • Scientific questions that can be addressed (for example the height-distribution of coarse and fine dust as in Figure 5: this has in turn an application on e.g. model evaluation – see O’Sullivan et al, https://doi.org/10.5194/acp-20-12955-2020 – and can bring whole new perspectives on understanding better the mechanisms of dust transport)
   • Observational requirements (accuracy and bias of the lidar observations of depolarisation) to be discussed in the framework of the state of the art
   • Potential application of the method on a global scale for existing lidar networks and satellite missions

MINOR PONTS:

See attached annotated manuscript which contains a number of suggestions and corrections.

Kind regards,

Franco Marenco