This paper describes a regional data assimilation experiment for aerosol using a novel height- and species resolved observational dataset. The authors evaluate the analysis against both assimilated and independent observations and conclude significant improvements can be found in the analysis vs the free run. The analysis shows sizeable redistributions of aerosol and an increase of total black carbon  which, as the authors show, strongly affects heating rates in atmosphere. This points to important limitations in our forward modelling ability.

The paper is very much in scope although one of its conclusions (that modelled and observed vertical profiles are very different with a strong impact on heating rates) will not surprise many people. However, the method to correct this is new and the paper describes the issue for a region very important for anthropogenic aerosol.  The paper is also very readable.

I have three main comments: 

1. The paper lacks details on the LETKF setup. While observation operators and background correction are  described the basic system is not. This is important as it is not even clear what sort of perturbation the LETKF uses. See further my questions below.
2. The papers suggests an observational uncertainty of 10% (Sect 2.2.1), yet the Kudo et al. paper finds uncertainties of 100% in the original dataset (Table 3), see also my questions below. The difference is a large one with important consequences. Maybe I misunderstand something but the authors need to present a clear narrative (Kudo is co-author on the current paper). I have trouble accepting a 10% uncertainty because already our best satellite AOD has 10% uncertainty (in long-term averages!) but the Kudo dataset is about vertically resolved, speciated extinction (daily!).
3. The paper describes a background correction scheme but provides little information as to how often and when/where this scheme is employed by the LETKF. The scheme is essentially a poor man's analysis update, equating the analysis to the observations without any attention to uncertainties. The presence of this scheme suggests that good agreement between the analysis and assimilated observations will never be in doubt. But is the combined system still a data assimilation scheme or only a form of blunt nudging? Is this background correction acceptable given observational uncertainties and ensemble spread? The authors need to provide more detail and discuss the simplification of data assimilation by their background correction more clearly than they do now.

I also want to point out that items 2) and 3) are related: the larger the observational uncertainty, the less truth worthy the background correction. 

I further have the following comments/questions:

p. 1, l. 31: induces -> induce

Section 1

p. 2, l. 41: "Elevated absorbing layers...lower atmosphere" this sentence is not clear to me, it seems that the two parts say almost the same, so why do you use 'whereas"?

p. 2, l. 46: I'm a bit surprised by the mention of water vapor absorption. Surely this happens at ()IR wavelengths but your abstarct talks about SW.

p. 2, l. 60: I would argue that CALIOP and CATS also suffer from limited spatial coverage. CALIOP has a beam width of 70m? Maybe the authors can be a bit more precise. The spatial coverage here is horizonatl spatial coverage.

p. 3, l. 86-91: The statement (that the problem is particularly severe over East Asia) is not supported by analysis or references. Please provide some, or be more cautious in your statement.

p. 4, l. 120-121: "Aerosols are parametrised as external mixtures ..." Are the sizes and standard deviations defined in WRF-Chem identical to those in CRTM? Especially older models tend to be inconsistent about such choices.

p. 5, l. 39: Can the authors provide a bit more detail about observational uncertainty? They assume 10% retrieval uncertainty but that can't be right. Especially because they break down extinction into different components. Table 3 in Kudo et al. (2019) suggests uncertainties of more than 100% in components like absorbing aerosol, dust aerosol. Assumed uncertainties in components will be important in the data assimilation step so I would like to ask for more detail from the authors.

p. 5, l. 142: it is very likley that the authors underestimate representation uncertainty with this method as observations tend to cluster and aerosol fields tend to be strongly correlated in space. I understand that better approaches are hard to come by but please discuss this. See also Rijsdijk et al. GMD 2025 for a similar problem with NO2.

p. 5. Sect. 2.2.1.: It seems to me the authors do not discuss how the WRF-Chem aerosol is mapped onto the CALIOP-MODIS components. Can they provide more detail? In particular, how well do WRF-CHEM assumed particle sizes agree with retrieved sizes per component? Same for refractive index per species. Both WRF-Chem and Kudo et al. make assumptions on refractive index. Are they the same? I later saw that you partially answer this in Sect. 3.1. Still, my question on sizes and refractive indices still stands.

p. 7, sect 3: Can the authors provide more detail on the LETKF system, especially the timing of assimilation? Does it happen every hour, or only at CALIOP overpass times? What is the time-window (4D-LETKF suggests there is a time-window in which obersvations at t will influence state at times before t). Also, how is the ensemble created? Are emissions perturb, or concentrations? What size of perturbations? Any spatial/temporal correlations in the perturbations?Also, how do the authors deal with boundary conditions (inflow from source regions outside domain).

p. 9, l. 206: "local patch center" has not been defined. Please rephrase. Only people familiar with LETKF will understand what it means.

p. 9, l. 215: "This strict variable localization... after data assimilation". If the observations of components were independent and the mapping from WRF-Chem to observations perfect, wouldn't the authors expect this to be unnecessary? Of course, nothing is perfect but I would appreciate it if the authors explain a bit more why this variable localization is necessary.

p. 9, l. 219: "severe model underestimations" does this happen only for component AOD or also total AOD? What causes it? The authors description is a bit vague. Does default WRF-Chem already underestimate AOD? How large is the spread in the emissions and component AOD compared to typical errors? A common solution to this is a pre-tuning step whereby emissions are scaled according to a mismatch between deafult forward run and observations.

p. 10, l 230: "outliers" so what do you do with outliers? I suppose they are not assimilated but I can't find this in the text. Please clarify.

p. 10, l. 231: "background ensemble factors are rescaled by dividing by this factor." So each member is rescaled with the samefactor. Please clarify this. Also, this implies that you correct the ensemble mean but the ensemblespread remains rather small. I guess that may be why inflation is later on needed? (In my experience, with perturbed emissions, inflation is seldom needed).

p. 10, l. 236: "while preserving the physical consistency of the ensemble". I think this background correction stratgey is a poor man's data assimilation tehnique. It ignores uncertainty in both ensemble and observations and just puts the analysis equal to the observations. It seems unsatisfying especially because the authors remain quite vague about how often this happens in the first place. So I would appreciate more discussion and explanation (see also previous questions). How often is this background correction triggered compared to a real Kalman update? Are there any patterns in this triggering (e.g. more over land, more in free troposphere than in BL etc)?

p. 10, l. 236: "physical consistency" please explain, the meaning is unclear to me. What aspect of physics do you refer to? Clearly no law of conservation is involved so I don't understand "physical consistency"

p. 11, l 291: "core_shell" this should have been discussed earlier in Sect 2 on data and methods. See also my previous comments on mapping of aerosol species from obs to GOCART. 

p. 11, fig. 3 I would suggest using logarithmic axes to bring out the region from AOD=0.01-0.1 better

p. 13, l. 317: "substantial improvement" please remind the reader that this is a self-validation; the authors are only testing with observations that were used in the assimilation.

p. 13, l 324: "system is difficult" -> "system has difficulty". Your background correction strategy is designed for this sort of problems, why does your system still have problems correcting the low bias?

p. 13, l. 325: "magnitude of lofted plumes" it would be interesting if the authors can supply some analyses of plume structure in obs and FR/DA. Is it possible to show curtain plots (latitude-altitude, averaged over longitude for E Asia)i for BC or something similar? Fig 3 and 4 provide average statistics so something that tells us more about how good DA reconstructs observed plumes.

p. 15, sect 4.2: It would be very interesting if authors can also provide an evaluation of the Kudo dataset with AERONET and ground-based LIDAR. This would help understand how much the validation of DA is driven by errors in the Kudo dataset vs errors in the assimilation itself.

p.20, l. 419: if we assume that the AERONET sites are relatively close to sources (closer than CALIOP), this suggests that emissions may be too high but lifetimes too short? If this idea has merit, please discuss it in the paper. 

p. 21, l 451: "traditional assimilation of total AOT merely scales" This is incorrect and depends strongly on the details of the assimilation technique. Even by assimilating only AOD can one change profiles and speciation because the AOD observations include locations both near and faraway from sources and so influence the analysis at different parts of the transport. In addition it is entirely possible (and has been  done many times) to include either/both speciation and profile into the statevector. I am not saying that speciated observtions (as in this paper) are not important (I think they are) but the authors' statement is simply incorrect.

p. 21, fig 12: please explain the downward spikes seen in SSA for the DA results in a), b) and d).

p. 22, l. 467: "warming suggests tha the assimilation effectively corrects" This is a really strange conclusion because you have no independent heat profile data to verify against. Also, the Da results have already been evaluated against independent AOD, extinction and SSA data.I suggest removing or completely rephrasing.

p. 26, l. 520: "the DA experiment succesfully recosntructed the vertical profiles of all four aerosol components". I think the authors overstate their results. First: there is no independent vertical profile data on speciation that confirms this result. Second: it is not a surprise that self-validation looks so good because the authors use a background correction scheme that makes the analysis identical to the assimilated observations. The authors should rephrarse their statement and clearly describe the limitations I just mentioned.

p. 26, l. 535: "internal mixing" while it is important to discuss this limitation in the Conclsuion I think it should already be discussed in Methods

The manuscript presents a highly relevant and ambitious effort to assimilate speciated aerosol vertical profiles from CALIOP-MODIS into the WRF-Chem model using a 4D-LETKF framework. Constraining the vertical distribution of distinct aerosol components is a well-known challenge in the aerosol modeling community, and the authors’ approach to explicitly optimizing scattering and absorbing species is commendable. The paper is generally well-written and addresses an important topic within the scope of the journal. I recommend minor revisions before publication.

Main Comments:

1. While I understand the engineering necessity of the background correction scheme (Section 3.3) to handle near-zero background spread, replacing the background ensemble directly with the rescaled observations completely bypasses the Kalman update. From a dynamical perspective, abruptly inserting a massive amount of aerosol mass (e.g., the missed 6 km BC plume) into the model state can cause severe "model shock." Since WRF-Chem is running with aerosol-radiation feedback enabled, this sudden mass insertion could generate spurious vertical velocity or artificial buoyancy anomalies in the subsequent integration steps. I recommend that the authors discuss whether any initialization techniques or relaxation timescales were applied to smooth this mass insertion. If not, please evaluate and discuss the potential influences introduced by this hard-replacement strategy.
2. Setting the observation error to 10% of the retrieved extinction is unrealistically low, especially for speciated retrievals where uncertainties often exceed 50%. In the LETKF framework, an artificially low observation error forces the Kalman gain to heavily favor the observations, which may partially explain the "near-perfect" self-validation scores (CORR = 1.0) alongside the bypass mechanism. The authors should justify this choice from a filter-tuning perspective. Was the 10% threshold chosen specifically to force the analysis closer to the observations due to persistent model negative biases? A sensitivity test using a more realistic observation error (e.g., 30% or 50%) over a short period would greatly strengthen the paper by demonstrating how the LETKF behaves when the observation and background errors are more balanced.

Specific Comments:

1. Line 118: The text mentions "aerosol-radiation feedback enabled." Does the FR (Free Run) also include this feedback? If so, the meteorological fields between FR and DA will diverge over the 25-day period due to different aerosol heating. Please clarify if the meteorology was re-initialized or nudged to ERA5 during the cycle to prevent chaotic divergence.
2. Section 3.2: The vertical localization length is set to 1 model layer. Given that WRF-Chem vertical layers stretch significantly with altitude (from tens of meters in the PBL to over a kilometer in the upper troposphere), a fixed model-layer localization might be too restrictive in the free troposphere and too broad in the boundary layer. Please comment on the impact of this choice.
3. Section 3.1: The authors mention that the GOCART scheme simulates dust in five size bins and sea salt in four size bins. However, the CALIOP-MODIS dataset provides a single bulk extinction coefficient for dust and sea salt, respectively. When the LETKF updates the state vector, how are the analysis increments distributed among these multiple size bins? Are the individual bins updated independently based on their respective background error covariances, or is the total mass increment simply distributed proportionally to the background mass fractions of each bin? Please clarify this technical detail.
4. Section 2.1: The manuscript highlights the successful reconstruction of elevated BC plumes originating from the Indian subcontinent (e.g., Figure 4c). Given that the Indian subcontinent is often located near the southwestern boundary of typical East Asian modeling domains, the treatment of chemical boundary conditions is critical. Please specify what global dataset (e.g., MOZART, WACCM, or CAM-chem) was used to provide time-varying CBCs. If idealized or climatological boundary conditions were used, could the severe underestimation of the mid-tropospheric BC in the FR experiment be partially attributed to missing aerosol inflow at the domain boundaries?