Review of the paper by Wei et al. ACP 2025

The paper presents an interesting analysis of measured absorption enhancement by black carbon particles mixed with other species. The data are interesting and quite valuable. However, several aspects of the manuscript are not well explained, and some are confusing or unclear. I think the authors can address most of these shortfalls, and if so, then the manuscript would deserve publication.

General comments

• The definition of “transition state” is vague, and it should be quantified. The criteria used are not clear.
• How the three cases (1,2, and 3) were defined is not clear.
• The link with local conditions, pollution level, and contribution from different sources is not well developed. It is probably possible and relatively straightforward for the authors to use existing monitoring data to corroborate some of their discussions. I would also suggest generating some more discussion of the back-trajectory simulations to determine transport path and time, and potential sources. The authors do show some of this work in the SI, but in the main paper, there is little to no mention, and more discussion should be added.
• The SI also shows an ACSM, which might provide further information that I did not see discussed in the paper. Maybe I missed it, but was Figure S7 based on the ACSM data? Maybe that could be made clearer in the SI as well as in the main text. Small note: In the same figure, CPAS should be CAPS (?)
• It is not clear to me what the “improved model” is and how it is operationally defined. More details should be provided on this topic as it seems to be central to the discussion.
• The literature cited is somewhat lacking and perhaps a bit biased; especially lacking is the comparison with other single-particle techniques such as microscopy.
• Even though the paper is mostly clearly written, the grammar should still be improved; some limited examples are provided in the next section.

Specific comments

• Line 35: space after models
• Line 51. I think Fierce’s paper also discussed the effect of morphological deviations at low M_R
• Line 86: “an BC” -> “a BC”
• Line 111: “was” -> “were”
• Line 120: How were the concentrations of PSL measured?
• Line 127: “a” in front of “single”. Also, what do the authors mean by “without any assumptions”?
• Line 129: “to compare the” -> “to be compared with”
• Line 134: Mie is good only for spherically symmetric particles. How do the authors account for that, considering the premise of the paper is the deviation from spherical symmetry?
• Line 137: The refractive index used here seems quite high with respect to other studies in the literature. Additionally, the coating is sometimes slightly absorbing, and that can make a difference, especially at shorter wavelengths. A sensitivity analysis using a range of indices of refraction would be helpful.
• Line 154: MAC units?
• Line 164: Why are these refractive index values different from those in Figure 137? Is it because of the wavelength? The wavelengths should be specified clearly in every instance.
• Figure 1: The core shell Mie model is for 200 nm, what is that a radius or a diameter, and is it mass equivalent, or something else? Also, why 200 nm exactly? More discussion on the model would be useful.
• Line 215: I would not use the word “closely” here; the agreement is reasonable, but not that close.
• Line 227: What does “at different period” refer to exactly? Perhaps “periods”.
• Line 232: Why log₁₀?
• Line 241-242: I am not sure what “due to stems” means.
• Lines 264-265: I am not clear how these ranges are defined.
• Line 265: I do not recall the authors discussing the pollution regimes of the three cases. I would give that more emphasis early on because that is probably at the root of the observed behaviors.
• Line 269: What do the authors mean by heterogeneous aging?
• Line 272: While plausible, this explanation (on why “BC required less coating material to evolve into a core-shell structure”) is not completely clear to me, and the authors might want to elaborate more.
• Line 292: Again, I think “closely” is too strong.
• Lines 300-302. I believe in the paper by Fierce et al., the discrepancy was suggested to be due to M_R heterogeneity but mostly for Large coatings, while for low coatings the deviations were associated with non-core-shell configurations, so I do not see a clear discrepancy between the two studies, on the contrary, it seems to me that the results are quite similar when considered for similar coating regimes.  
• Figure 4(b), 4(c), and 4(d), what is on the x axis? Please put an axis title and units if applicable.
• Line 323: Why inorganic specifically? Why not also organics?
• Line 337: The authors should clearly describe the “improved method”. Here, it is not clear at all what that is. How was the fit performed, and what did they do with the fit?
• Lines 360 to 368: How do the authors suggest developing such a unified model?
• Figure S2: It is not clear how the CPC would measure a size distribution, being a simple counter. The caption mentions a DMA; perhaps that should be clearer from the legend. What are SCHG and BBHG (scattering and broadband high gain?). Spell out acronyms in the caption.
• Figures S4 and S5: the signal ranges are very different. Why is that? Can the nephelometer and the CAPS measure scattering coefficients below 0.01 Mm^-1 accurately and precisely? That is hard to believe. Also how were the Mie simulations being informed, in terms of concentrations, size, and index of refraction?
• Figure S7: What does the horizontal pink dashed line indicate, the mean E_abs?
• Figure S8: Some more information is needed. How were the trajectories being calculated? What is the time span, what is the elevation used, can the authors also provide vertical trajectories to see whether the air masses are coming from the boundary layer or from aloft to understand if it is near or long-range transportation?
• Figure S9: Are these based on the SP2?
• Figure S10: The units on the x-axis are not critical, but still, it would be nice to have them.
• Figure S11: Units on x axes (fg?).

Some limited references that might be of relevance:

1.    Beeler, P., et al., Light absorption enhancement of black carbon in a pyrocumulonimbus cloud. Nature Communications, 2024. 15(1): p. 6243.

2.    Ueda, S., et al., Light absorption and morphological properties of soot-containing aerosols observed at an East Asian outflow site, Noto Peninsula, Japan. Atmos. Chem. Phys., 2016. 16(4): p. 2525-2541.

3.    China, S., et al., Morphology and mixing state of individual freshly emitted wildfire carbonaceous particles. Nature Communications, 2013. 4.

4.    Cross, E.S., et al., Soot Particle Studies—Instrument Inter-Comparison—Project Overview. Aerosol Science and Technology, 2010. 44(8): p. 592-611.

5.    Corbin, J.C., R.L. Modini, and M. Gysel-Beer, Mechanisms of soot-aggregate restructuring and compaction. Aerosol Science and Technology, 2022: p. 1-48.

6.    Adachi, K. and P.R. Buseck, Changes of ns-soot mixing states and shapes in an urban area during CalNex. Journal of Geophysical Research: Atmospheres, 2013. 118(9): p. 3723–3730.

7.    Adachi, K., S.H. Chung, and P.R. Buseck, Shapes of soot aerosol particles and implications for their effects on climate. Journal of Geophysical Research-Atmospheres, 2010. 115.

8.    Adachi, K., et al., Mixing states of light-absorbing particles measured using a transmission electron microscope and a single-particle soot photometer in Tokyo, Japan. Journal of Geophysical Research: Atmospheres, 2016. 121(15): p. 9153-9164.

9.    leviChang, H. and T.T. Charalampopoulos, Determination of the Wavelength Dependence of Refractive-Indexes of Flame Soot. Proceedings of the Royal Society-Mathematical and Physical Sciences, 1990. 430(1880): p. 577-591.

10.    Moteki, N., Measuring the complex forward-scattering amplitude of single particles by self-reference interferometry: CAS-v1 protocol. Optics Express, 2021. 29(13): p. 20688-20714.

11.    Liu, S., et al., Enhanced light absorption by mixed source black and brown carbon particles in UK winter. Nat Commun, 2015. 6.

The manuscript treats an important aspect of black carbon optical properties with innovative techniques. Overall, the topic and novelty fulfil the requirements for ACP publication. Some work still to be done improve the readability of the manuscript and especially ensure that robustness of the measured properties. The article requires consistent modification.

NOMENCLATURE AND READABILITY: The use of abbreviations and symbols requires careful attention. Several parameters (particularly those distinguishing measured from modeled quantities) are difficult to follow, which hinders comprehension, especially in the results section. I strongly recommend introducing a summary table listing each property, its abbreviation, and whether it refers to a measurement or a modeled value. Improving consistency here would greatly enhance clarity for readers unfamiliar with the measurement framework.

INSTRUMENTAL DESCRIPTION AND UNCERTAINTIES: The methodology section currently lacks sufficient citations and discussion of measurement uncertainties. Given that the study combines multiple instruments in a novel configuration, these details are crucial. The uncertainties of the CPMA–SP2 tandem system, as well as of derived quantities such as Mₚ and M_BC, should be clearly stated and discussed in the context of previous literature. Since many key quantities in the analysis are expressed as ratios, unquantified uncertainties may propagate and influence the reported variability. In line with other reviewers’ remarks, I encourage the authors to describe the CPMA–SP2 system and data processing steps in greater detail, including how calibration and error propagation were handled.

RESULTS AND INTERPRETATION:The results section shows promising potential for impact, but several points require clarification. The authors could strengthen the manuscript by expanding the discussion on how the proposed “transition-state” correction scheme might be generalized to other atmospheric environments. For example, conditions in rural or biomass-burning regions, or during other seasons, may produce distinct coating compositions and morphology evolution pathways. Explaining how the correction parameters (e.g., MR thresholds or morphology indicators) could adapt to such conditions would enhance the broader applicability of the method. The method for defining the three “cases” should also be revisited. It appears that only Case 2 represents a specific or anomalous event compared to the rest of the campaign. I suggest first describing the overall meteorological and bulk aerosol conditions and then examining how the optical properties vary under those regimes. This would provide a more physically grounded interpretation of the case classification. At present, the combined issues of unclear nomenclature and insufficient methodological detail reduce the understanding of the results, being the ultimate limiting factor of the manuscript.

SPECIFIC COMMENTS

L1: title. I am not convinced by “heterogeneity”. What does it mean in this context? It is a very general term that, alone, does not convey a unanimous message.

L35-38: Eabs is not contextualized, not properly described. Enhancement with respect to? Please provide a short description.

L51: what do you mean with heterogeneity?

L67: please avoid the use of  “fortunately” , it undermines the preparation and thoughts behind your research. Leaving  the reason of the positive outcome of your work to luck.

L80-84. If available, I suggest adding 1 or 2 references describing the site and its representativity.

L86-109. I suggest describing a bit more each instrument alone. With the use of references, which is limited. Here some old works about SP2 describing its principle: (Stephens et al., 2003; Moteki and Kondo, 2010) and calibrations: (Gysel et al., 2011). I suggest  a recent paper exploring the operational limits of the SP2 (Schwarz et al., 2022).  This is the major reference of the CPMA: (Olfert and Collings, 2005).  For the tandem combination of SP2 with mass analysers I suggest a relatively old review (Cross et al., 2010) and a more recent set of papers (Liu et al., 2022; Naseri et al., 2022; Zanatta et al., 2025). DMT 2011. This is an odd reference. The ACQUADAG scaling factor to fullerene should be slightly better accounted for. DMT 2011 is and odd reference. The original reference should be (Baumgardner et al., 2012; Laborde et al., 2012).  Please do the same for the ACSM. The CAPS-SSA is fully detailed by (Modini et al., 2021). Overall, these works report all the error associated with the single measurements, which will propagate substantially for the application intended in the current manuscript. None of these are described.

L93: I would expect the SP2 showing the multi charged particles. How exactly was the mass MBC calculated?

L115. What model and company? Please be consistent with previous notation.

L122: CAPS and nephelometer may well respond to PSL, especially small PSL. Truncation error may become more and more important with larger particles and especially irregular particles…such as ramified fresh BC. Please provide a small statement about it. Was truncation corrected?

L127: Well, we “assume” that everything is working properly. This is why is important to estimate, even roughly, the uncertainty.

L132-133: I have a couple of questions here. The CPMA is capable of selecting particles based on their mass to charge ratio. Hence, it is recommended, even by the manufacturer, to run the CPMA after a neutralizer/charger. From the schematics of Figure S1 it looks like there was no neutralizer. What it is the additional uncertainty of running  the CMPA-SP2 setup without a charger? Single and multi-charged peaks, should be visible in the mass distribution provided by the SP2. I wonder if the authors quantified the single particle BC mass (MBC, by fitting the SP2 mass distribution, including only the first peak (single charge) or fitting the full distribution). This technical detail may influence all the result sections. Hence need to be fully and properly described.   Regarding the sampling collection. Unfortunately, Figure S2 shows that the counting efficiency of the SP2  is far from 100%, especially below 100 nm (Figure S2a). It is also surprising that the SP2 counts systematically more than the CPC. I presume that some setting in the SP2 were not properly configured or that the CPC had some counting issues. Moreover, why the two incandescence detectors should  have a different (linear and non-linear) mass/incandescence relationship?

L140, why distorted. It is attenuated due to the evaporation of absorbing-refractory material.

L142-146:  the LEO-fit relies on many assumptions, as correctly stated by the  authors. It would be nice if they could elaborate, shortly, about the reason behind these choices. Moreover, with a similar number of assumptions (density of coating and BC cores), the optical coating thickness could be derived directly from the Mp  and Mbc was this performed? Are the results coherent?

L149: define the MAC.

L154: I like the approach of deriving the MAC of uncoated BC using this extrapolation. However, this MAC (no units) for uncoated BC results to be slightly higher than previous estimations in European urban (Savadkoohi et al., 2024) rural (Zanatta et al., 2016) and the canonical 7.5 m/ g of (Bond and Bergstrom, 2006). This could also be due to the high variability of MAC itself across sites and seasons, but also to strong  uncertainties related with MAC (absorption and BC mass) and bulk MR (width of  the distribution of particles exiting the CPMA and method to quantify the single particle mass with the SP2).  Overall,   I notice a lack in providing context to these findings and assumptions. The MACBC_core is fundamental to all the results presented in the paper, hence, even small errors may substantially modify the quantification of the enhancement.  The authors must provide more details on their methods and uncertainties, and put all of these consideration with the context of recent literature.

L169-175: I am genuinely confused on how the MACbc introduced in equation 3 was calculated. Use a logic order when presenting variables. Is the MAC of equation 4 the same presented in equation 3?

L174: The nomenclature is a bit confusing here. MACBC-core of line 174 is the same used int Equation 3 ? Or the MA_core, presented in Line 154 is used in equation 3? So, the “Mie MACBC_core” is it similar to 9.08 m2 /g. This aspect is extremely important and influences with a different weight MACMie and MAC observed with a different weight, especially in figure 2d where the delta enhancement is presented.

L188: At what wavelength are these values provided. Could  the authors state something about the absorption enhancement at different wavelengths? The high presence of organic material may change the Eabs at lower wvalenght?

L220-221:  I recommend caution when mentioning morphology, especially in a section title. This scattering cross-section ratio is a far approximation for morphology  assessment. It may be a proxy, but nothing more and must be confirm by real morphology observations such as microscopy fractal dimension or, at least DMA/CPMA density/fractal exponent measurements.

L222-223: what is the meaning of the sentence?

L239: The authors states that the difference between observed and modelled enhancement depends on the variability  of the standard deviation of MR. First why the log10(Mr) was used ? Second, I all honesty, it is difficult to observe any sort of correlation in the scatterplot presented in figure 2d.  Especially considering that  correlation coefficient and slope changes substantially among the periods. In my opinion, Figure 2s does not support the claims of the authors.

L254: please provide the wavelength

L252-276: although the results shown in figure 3 are interesting, this section is very confusing. It is hard to understand what causes the decrease in the transition regime. Try to restructure your though in a more logic process. Could this “transition state” represent the compaction due to coating formation. This sort of natural process will reduce the optical and geometrical cross section of the particles. It is usually observed in chamber studies (e.g. Schnaiter et al., 2005; Zanatta et al., 2025)  and rarely, up to my knowledge, observed in ambient conditions (Bhandari et al., 2019). This process description could be developed further.

Section 3.3 soffers a similar issue with readability. I am not fully convinced by the reasoning behind the period separation. Only period 2 looks different from the others.

F1: are these enhancement measured all at the same wavelength?

F2: please improve the labelling of the axis. Number counts and SD of…?

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