• General comment: This is an interesting work, based on the observation of different patterns in aerosols associated with different wind trajectories. However, some clarifications are needed. Section 3.4 about optical absorption should be revised. Although English is good in general, grammar should be revised. Notation is not always defined or is not self-consistent. Structure (main manuscript/SM) should also be revised.
• Specific comments: Segregation of information into the Supplementary Material should be done when this information is not essential for understanding the study. In this case, the information in the SM is essential to follow the main manuscript. Authors are suggested to reorganize the information.
• Introduction: This reviewer does not agree with some conventions often used in environmental articles, such as the equivalence between black carbon and elemental carbon (BC is a carbonaceous combustion-derived aerosol, while elemental carbon is the major chemical component of BC, but also of any organic material), or the list of soot sources (why fossil fuels and biomass??; any liquid biofuel, electrofuel, or non-biologic waste material will also emit soot when burned).
• Introduction: This reviewer does not agree that “simulating soot climate effect is readily achievable in models”, as stated. The variety of sizes, shapes, compositions, and nanostructures affect the optical properties of soot and makes the simulation very difficult.
• Section 2.2: If OM/OC ratios in Chinese cities is assumed as 1.91, what organic matter is the remaining 0.91/1.91? Why
• Sections 2.2 and 3.2: TEM operates under high vacuum. Therefore, evaporation or sublimation of coatings could occur even in “conventional TEM observations”. What is the change in the beam power to distinguish between “enhanced electron beam observations” and “conventional observations”, and thus between enhanced and conventional absorption? Could authors include TEM images of the same particle before and after enhancing the beam power? Visible bubbles observed in Figures 3 and 4, indicating evaporation, are declared to correspond after enhancing power, but how do these particles look like before? Are diameters “Dp” those obtained with TEM under conventional mode and “Dc” those obtained under enhanced electron beam? Please clarify.
• Sections 2.2 and 3.2: What do authors exactly mean by “mixing states” of soot particles? Is it an appropriate name? Based on Text S1, it seems that they refer to chemical composition. However, based on Section 3.2 and Figures 3 and 4, it seems that they refer to bare-like, partly-coated or embedded. Please correct or clarify.
• Section 2.2: Equations 4 to 7 are written without a brief explanation of their meaning. Authors should at least explain that ignoring the overlap (or sintering or interpenetration) between monomers would lead to underestimation of the fractal prefactor of the power-law relationship (eq. 4). Moreover, publications after 1997 have demonstrated that also this prefactor (not only that in eq. 5) is highly affected by the overlap parameter (see, e.g., Powder Technology 271, 141–154 (2015)).
• Section 2.3: Parameters “n” and “W” in equation 9 are not defined. Please check uniformity in the notation.
• Section 3.1: In Figure S4 the content in EC (supposedly associated with soot) is very minor (purple). On the contrary, in Figure S5, the percent of soot-containing particles is very high (light blue). How do these results match?
• Section 3.3: What is, in the opinion of authors, the dominant reason for the increase in the size, the number of soot cores, the Dp/Dc ratio, and the fractal dimension of soot structures: coalescence between agglomerates (entrainment) or breakage of agglomerates inside the aerosol (collapse)?
• Section 3.4: This reviewer can understand that the energy adsorbed is reduced for the sea pathway with respect to the inland pathway, and even that multiple cores may also contribute to reduce absorption. But does not understand why the energy absorbed from embedded particles is higher than that absorbed from soot cores (Figure 10a). The refractive index of soot is much higher than that of coatings (and specially its imaginary part, related to attenuation of light). Consequently, the ageing process should lead to a decrease in the energy absorbed. Please, revise, or explain better.
• Technical corrections: please correct “If the high-pressure system located” to “If the high-pressure system is located”; “Obviously, there was a bench of data” to “Obviously, there is a bench of data”; “However, transboundary haze pollutants crossed the East China Sea remain unexplored” to “However, transboundary haze pollutants crossing the East China Sea remain unexplored”.

The manuscript by Zhang et al. investigates two different soot aerosol aging processes by comparing the properties of particles that are transported over land and over the ocean. The authors utilize measurements of particle morphology, number of soot cores and coating thickness, and report differences in optical properties.   Overall, it was found that particles that were transported via the sea pathway, and likely underwent aqueous-phase or cloud processing, had an increase in soot core number and a decrease in absorption enhancement compared to particles that were transported over the land, where heterogenous oxidation dominated. 

Overall, the study is well conducted, clear, and of interest to the ACP community.  I would recommend publication after addressing a few minor comments.

1. The authors primarily discuss environmental conditions (cloud processing, RH, etc) as what is causing the differences between the two aging pathways. Although this evidence is convincing, there are likely also significantly different emissions mixing with the haze plume during transport over land than over the ocean. This is briefly mentioned as a possibility at line 95 but not referred back to in the results section. Can the authors comment on if these differences and if they have implications on the observations or results.
2. Line 327: Figure 3 and 4 show particles with soot cores very close to the particle edge. How exactly are partly-coated and embedded particles differentiated. Is there a specific threshold for how much soot is exposed for it to be considered partly-coated? Similarly, how did the authors categorize multi-core particles where individual cores were embedded and partly-coated in the same particle. 
3. Line 392: Are the differences in coating thickness between NCP and YRD statistically significant?
4. Can the authors expand on their discussion of the water rim observed in some particles, as this seems to be an important piece of evidence for aqueous phase processing (i.e. line 427). It would be helpful to clarify if this is a marker for particles that have undergone aqueous-phase processing (as mentioned at line 431), or for particles that contained an aqueous-phase when analyzed with TEM (line 429).  Put another way: If the particles underwent aqueous-phase processing during transport, then were subjected to lower humidity conditions and effloresced, would the rim still be present. 
5. Line 437: Is there satellite or meteorological evidence of clouds being present along the back trajectory of the airmass. If possible, It would be useful to differentiate between cloud processing and high humidity (but still subsaturated)  
6. Line 512: Can the authors clarify why entrainment of multiple soot cores results in lower ΔE_abs/Δ(D_p/D_c).
7. Most figures (Figure 2, 4, 5, 6, 7, 8, 9) have panels for the results of each pathway, however it is not immediately clear which one is which. Although this information is in the caption, I would recommend labeling the row or panels with the different pathways.

Minor Comments:

- Line 193: When calculating D_p/D_c, how are multiple soot cores handled. Is ESD_soot the sum of all soot cores?

- Line 278: It would be helpful for context to include an average (or range of) transport time based on the back trajectories. 

Typographical

Line 98:  “…exerting favorable effects on global warming in the atmosphere”

• I would recommend changing from “favorable” to “positive radiative forcing” or similar.

Line 293: “These results suggest that massive primary and secondary aerosols including EC (i.e., soot) were transported from the NCP to the YRD under cold fronts, both through the inland and the sea pathways”

• The word “massive” here is confusing. I would recommend changing it unless the authors are referring to the size of the particles.

Manuscript: Disparate evolution mechanism and optical absorption for transboundary soot particles passing through inland and sea pathways (Zhang et al.,)

Review of manuscript:

Understanding how aerosol particle age during transport is critically important for improving model performance yet still suffers from the paucity of field data that can guide model development.  The current manuscript by Zhang et al., provides much needed property and aging data on PM2.5 particles by being able to compare the pathway impacts over inland vs the sea.  To carry out this study, the authors examined the microphysical and optical properties of haze particles from the North China Plain (NCP) to the Yangtze River Delta (YRD) where cold fronts exhibited two different pathway: an inland path and a “sea” path that took the air mass across the East China Sea.  The authors report that the “dryish” inland path favors a heterogeneous-centric aging pathway with single-core embedded soot, whereas the sea pathway, with its concomitantly very high RH and cloud processing favors entrainment and coalescence resulting in the production of super micron particles characterized by multiple soot cores inside large droplets/residuals that exhibit a lower absorption enhancement than that calculated for the inland pathway particles. This manuscript tackles an important problem with a modern, multi-method approach and yields novel, physically meaningful insights about how transport environment affects soot aging and absorption.  This manuscript is recommended for publication AFTER some moderate revisions that are focused on clarifying the uncertainties and representativeness in the measurements, greatly increasing the language transparency in discussing the cloud process aging as the dominate mechanism vs. other high RH processes and increasing the narrative on the underlying modeling assumptions. These are discussed below.  Also, the narrative is convoluted at several points within the manuscript and thus the authors are encouraged to have the manuscript grammar reviewed. 

The analysis rests primarily on two winter haze events (2017, 2020). These events appear well chosen and documented, but they still represent a limited sample of meteorological regimes.  How representative are these case studies and to what extent are they generalizable to other years, and source composition (e.g., wildfire aerosols vs fossil fuel)? It is assumed that the transport trajectories indicate that the haze plumes stayed in the boundary layer and did not punch through to the free troposphere.

While the Reviewer appreciates the effort of analyzing 3642 particles, the authors need to ascribe uncertainties/confidence intervals on all reported fractions (e.g., 62 vs. 67%; 71 vs. 72%) and on Dp/Dc and Df.  It is also suggested that a statistical significance test be performed in the comparison between inland and sea cases.

While the observation of water rims and droplet-like morphologies are compelling indicators of aqueous processing, they do not uniquely prove that cloud processing is indeed the route.  One could observe similar water rims from deliquesced aerosol under very high RH below cloud.  Indeed, the latter only requires a very high RH condition, similar to that reported, whereas the former requires supersaturation conditions for cloud droplet formation, which is not discussed in the manuscript. Thus, the authors need to clarify the distinction between in-cloud vs. sub-cloud aqueous processing as opposed to simply citing “cloud process”.  Similarly, while it is reasonable to assumption that multiple cores (2 - 3) per particle are primarily due to cloud entrainment and collision-coalescence, other pathways (e.g., coagulation in a wet aerosol layer, co-injection and growth of BC-rich, organic-rich droplets) could contribute.  Therefore, the authors are encouraged to provide a narrative (argument) that simple coagulation of soot-containing particles in a high-RH boundary layer is insufficient to produce the observed size and multicore distributions thereby supporting the proposed cloud droplet pathway.  Similarly, the authors are encouraged to be more tempered with their statement (page 20; lines 550 - 551) that “cloud process aging under extremely high RH became them major evolution mechanisms.”  An extremely high RH environment does not necessarily mean a cloud droplet environment (supersaturation conditions). 

While Dp/Dc is conventional for submicron size particles with a single-core BC, it is not the most robust choice for the super-micron, cloud-processed, multicore particles that dominate this study.  In this size regime that is the focus of this study, Dp and Dc are both equivalent diameters derived from 2D projections of highly irregular, droplet-like particles and compacted aggregates.  A major consequence of this is that Dp/Dc becomes strongly sensitive to particle morphology, orientation on the substrate, and, potentially, how the particle dried.  Thus, the authors are encouraged to consider using the mass (or volume) ratio of coating to core, which is particle morphology agnostic.  As a added benefit, the EMBS–DDSCAT framework used by the authors provides explicit core and matrix volumes for the modeled particles, thereby making it straightforward to examine optical enhancement versus coating:core mass (or volume) ratio instead of versus Dp/Dc.  Finally, as cited above, error analysis is strongly suggested for this metric.

There is the implicit assumption that the coatings are non-absorbing (1.53+0i).  While this might be appropriate or sulfate/nitrate rich shells it may not be nearly as robust if organic coatings contain brown carbon.  Given that the authors are focusing on relative effects of multicore geometry vs. coating thickness, this may be an acceptable assumption, but they are encouraged to explicitly cite this simplifying assumption.  Further, a sensitivity analysis as function of center vs. periphery vs. random position is encouraged to support the robustness of a 72% reduction claim.

 

One of the take-home messages of this paper is that ΔEabs/Δ(Dp/Dc) is reduced by  ~72% for sea-path soot because cloud processing generates multicore particles.  This result is a model-derived result.  Thus it might be useful to emphasize that ΔEabs/Δ(Dp/Dc) is a conceptual metric that depends on the chosen definition of Dp and Dc (e.g., equivalent sphere vs. outer droplet edge, etc.).  This would underscore that while model–model comparison is likely robust, model–measurement comparison would likely require careful matching of definitions.

This reviewer was surprised by the rapid growth for the inland-route particles reported to reach 0.5–0.7 µm within a single transport episode.  This is much larger than typically observed for non-cloud, early-age haze.  To what degree is this a reflection of measurement bias - either through choice of methodology and/or selected size range vs actual growth that reflects intense secondary production?  This is not to say that measurement bias invalidates the inland–sea comparison, but they suggest that the absolute size and coating metrics should be interpreted cautiously.  The authors are encouraged to talk about this, especially in their comparisons with previous results that focused on sub-micron particles.

Finally, this reviewer would also like urge caution on any quantitative comparisons to the submicron BC literature.  It is well-documented that sub-micron soot acquires nm-scale coatings through condensation and heterogeneous chemistry with concomitant restructuring processes, whereas the super-micron particles, the size regime that this paper is focused on, form through cloud activation, aqueous growth, and droplet-scale coalescence, requiring a very different aging pathway. As a consequence, caution needs to be exercised when comparing metrics like Dp/Dc, Df, and absorption enhancement from one regime to the other.  Hence, the authors are encouraged to be explicit in treating their comparisons with sub-micron studies as qualitative.

Specific items:

Page 6, line 155;  “…sampling duration of individual particles needs to be adjusted from 30 s to 15 min according to current PM2.5 concentrations.”  Please cite the concentration range that dictated sampling durations that spanned the 30-sec to 15-min range.

Page 15 (line 406)/Page 16 (line 407-408): “Soot particles have been demonstrated to promote the formation of secondary aerosols around them via heterogeneous or aqueous-phase reactions”.  Soot is not a catalyst as implied in this sentence.  Soot is chemically inert.  Their primary role is as a non-reactive, insoluble substrate upon which material can be condensed onto.  Please reword.   

Figure 7:  Please make the scale on the ordinate the same.  It will help underscore just how difference the two ratios are.  Also, as stated above, the authors might be serious consideration for using the mass ratio instead of Dp/Dc due to its independence of particle morphology.