Li et al. measured water-soluble organic carbon (WSOC) in both gas and particle phases using online and offline measurements over a one-month period in Spring in Shanghai. The author compared measurements between dust storms (DS), haze events, and clean periods. They claimed that high aerosol pH modulated the gas-to-particle partitioning of WSOC during the DS periods and found that DS led to remarkable increases in light absorption due to high concentrations of nitroaromatics, imidazole and water-solute organic nitrogen at the coarse mode.

The study focuses on a short dataset spanning only one month, and the discussion is based solely on the periods of interest that are 3-5 days long. Particularly, they only captured one episode of a dust storm. I do understand that dust storms do not occur with high frequency within one month. My biggest concern is that the levels of detail and discussion are not convincing enough for a publication on ACP. Therefore, I would suggest that the current version of the manuscript be rejected.

Major Comment

1. Length of the dataset: The study focuses on a dataset with nearly 1 month and discusses three measurement periods of interest (i.e., dust storm, haze event, and clean period). Each measurement period of interest spans 3 to 5 days. Although some of the analyses appear to be technically sound, I believe the sample size is too small to draw a firm conclusion. The current level of discussion is too simplistic and vague to capture the interest of the atmospheric science community. One example is that there are no details about what compounds contribute to the high MAC during periods impacted by dust storms.
2. Table 1: It is good to have Table 1 to summarise the statistics for different measurement periods. When reading the details in Sections 3.1 and 3.2, I found it challenging to keep track of the associated values in Table 1 without searching through the rows one by one. I recommend simplifying Table 1 and presenting only the relevant results in the main text while moving the current version of Table 1 to the supplement.
3. Sections 3.3 and 3.4: What is the non-dust storm period? Is it equivalent to the haze event plus the clean period? In Sections 3.1 and 3.2, you compare the dust storm with haze event and clean period. However, in sections 3.3 and 3.4, you compare the dust storm periods with non-dust storm periods. Importantly, there is no definition for non-dust storm periods. I am very confused about the consistency between different sections in the manuscript.
4. F_p: The F_p describes a compound's partitioning between the gas and particle phases. During DS periods, the authors claim the high pH is the main driver when ALWC is low. By definition, the F_p is governed by the effective saturation vapor pressure and aerosol mass loading (Lutz et al., 2019). When the PM₁₀ loading is sufficiently high at the DS periods compared to other measurement periods, how can you be sure that high pH is the only key driver of F_p? Discussions are needed regarding the effect of high aerosol mass loading on F_p during DS periods.

Minor Comment

1. Lines 52: Specify what the anthropogenic gas pollutants are.
2. Lines 66: What is “such a change in the East Asia atmospheric environment”?
3. Lines 99 and 103: How many PM₅ and PM₁₀ filter samples have been collected?
4. Lines 120-127: What are the identified nitroaromatics and eight imidazole compounds?
5. Lines 139–141: Is it your own way of defining a haze episode? I found there is a different definition of haze episodes in Dai et al. (2021). If so, please provide a brief description of how it differs from previous studies.
6. Figure 1: Improvements are needed to enhance the readability of the plot. First, you should provide spaces between each subplot. For some subplots, I am unable to determine whether the y-axis starts at zero. Lines should be thicker, and please avoid using red and green. For Na⁺ , Mg²⁺ , and Ca²⁺ , I would create a subplot for them. The same applies to NH4⁺ and Cl^-. I cannot identify any trend regarding these species, even with zooming in.
7. Table 1: Provide two additional rows for SNA, one for its mass loading and another for the mass contribution to PM₅.
8. Lines 162 – 163: Please discuss why there is no correlation between PM₅ and WSOC_p in DS.
9. Line 205: I cannot see how the uptake of acidic organics is favoured by dust. What is it based on?
10. Lines 246 and 249, Figure S5: The discussion is based on the statics of five points for NDS and DS periods. I am concerned with the robustness of the statistics. When examining other figures (e.g., Figures S1 and S2) for statistical analysis, I noticed that more data points are included.
11. Line 252: How can you determine that the coarse particles are enriched with CaCO₃?
12. Lines 259 – 263: I do not see the connection between the two sentences. The former is on the discussion about the NDS periods, while the latter is on the discussion on dust surfaces.
13. Figure 4: Similar to the MAC profile of Tengger Desert PM₁₀, could you please include shaded areas for the MAC profiles of other samples?

Technical Comment

1. Line 69: Could you use an alternative word instead of “wetted dust”?
2. Lines 110 – 116: The sentence is too long to read. Please split it into two or more.
3. Line 117: Give details about the liquid waveguide capillary UV–Vis spectrometer.
4. Section 2.3: You should provide the citation from the original papers about ISORROPIA-II, but not three papers in a row from the same group.
5. Figure 2: Provide details about organic acids in the caption.
6. Figure 3: What are the dashed lines and filled areas for? Which one is the measured size distribution?
7. Figure S3: Are these the normalized size distributions?
8. Figure S4: Could you please include the error bars?
9. Line 315: Is it supposed to be NH₄⁺?
10. Lines 317 – 319: What are the studies from the USA and other developed countries for comparison?
11. Table 2: Include the standard deviation for Table 2.

References

Dai, Q., Ding, J., Hou, L., Li, L., Cai, Z., Liu, B., Song, C., Bi, X., Wu, J., and Zhang, Y.: Haze episodes before and during the covid-19 shutdown in tianjin, China: Contribution of fireworks and residential burning, Environmental Pollution, 286, 117252, 2021.

Lutz, A., Mohr, C., Le Breton, M., Lopez-Hilfiker, F. D., Priestley, M., Thornton, J. A., and Hallquist, M.: Gas to particle partitioning of organic acids in the boreal atmosphere, ACS Earth and Space Chemistry, 3, 1279-1287, 2019.

Gas-to-particle partitioning of organics is a key process in secondary organic aerosol (SOA) formation. This manuscript presents field measurements of water-soluble organic carbon (WSOC) in both gas and particle phases, and investigates the characteristics of the particle-phase fraction (Fp), its potential formation processes, optical properties, and size distributions through case analyses. The authors suggest that physicochemical properties such as aerosol pH, aerosol liquid water content (ALWC), and particle composition play dominant roles in governing WSOC formation and Fp dynamics. The manuscript fits well within the scope of Atmospheric Chemistry and Physics (ACP), and the writing is generally clear. However, to support the conclusions more convincingly, the manuscript would benefit from a more thorough and quantitative discussion of the Fp dynamics, detailed analysis of WSOC measurements and chemical composition, more comprehensive characterization of particle size distributions, and improved evaluation of aerosol pH. Therefore, I recommend that the manuscript be reconsidered for publication after substantial revision and inclusion of the necessary details and discussions.

Major comments:

1. The WSOC data are central to the conclusions of this manuscript. However, the authors only briefly cited previous literature to describe the measurement methods. Detailed descriptions of both the offline and online WSOC measurement techniques, including sampling protocols, instrument calibration, detection limits, and potential uncertainties, should be clearly provided. In addition, during dust events, the particle mass is primarily dominated by coarse-mode particles. It is unclear how the use of a 2.5 μm cutoff inlet (PM2.5) can adequately represent the WSOC associated with dust particles. The authors should justify the representativeness of the PM2.5 sampling approach for characterizing WSOC during dust episodes or provide supporting data to address this limitation.
2. The pH calculation is based on the ISORROPIA-Ⅱ, but the basic evaluation of the predicted and observed parameters (such as NO₃^-, NH₃, etc) is not given, which is important for the model performance. In addition, RH is less than 30 in dust haze, which would introduce much uncertainty for pH calculation. It caused the high pH, up to 7.5, and this value is stable. However, during high Ca²⁺, indicator of dust episode, pH is comparable to haze and clean days. The more detailed discussion should be added to clarify this.
3. During the chemical analysis, the organic acids, NACs and IMs are detected. However, the detailed discussion is not given, which is important for WSOC Fp and dynamic characteristics. The Fp and gas-to-particle partitioning (kp) depend on the chemical properties of organics, aerosol components, particle phase, etc. In this manuscript, the authors just discussed the influences of inorganic components. The driving impacts of organics and particle phase was not considered. It should be added.
4. The size distribution of WSOC, NACs, etc. have been discussed, but the measurement of size distribution was not given. It should be added.

Specific comments:

1. In the abstract, it mentioned the time resolution of WSOC is 1h, but it is 3h in the method. Please clarify it,
2. Line 62, the “NOx” should be replaced with “NO_x”. Please checked all the upper and lower superscripts of the article.
3. Line 153, the author stated a “significant formation of SNA”. Once the term of significance was used, the statistical and significance analyses are necessary. Please add it. In addition, the Ca²⁺, as the indicator of dust, peaked at a short time, indicating minor influence of dust, not lasting three days. Please clarify it.
4. In lines157-168, the measured average WSOCp is about 2 µgC m^-3, but in Table 1 and 2, the total carbon of oxalic acid, Pyr, NACs and IMs are large than the average WSOCp. Please checked it.
5. In section 3.2, the author discussed driving factor of WSOC partitioning. In previous study (Ma et al 2022), it has reported that the particle phase would influence the OVOCs partitioning. For example, when ALWC was over 15 µg m^-3, as indicator of liquid phase for particles, it would weaken the gas-to-particle partitioning of OVOCs with kp>10^-5. In this manuscript, the author just discussed the general WSOC partitioning, which was determined by the chemical components. The more detailed information is needed.
6. In lines 196–205, the authors suggest that aerosol pH is a key factor influencing WSOC partitioning during the DS period, based on correlation analysis. However, further clarification is needed. During DS, Ca²⁺ and Mg²⁺ are the dominant cations, whereas during HE, NH₄⁺ predominates. This shift in ionic composition likely alters aerosol hygroscopicity, thereby affecting aerosol liquid water content (ALWC). The manuscript posited out that in the HE period, higher ALWC dilutes H⁺ concentrations, leading to higher aerosol pH, whereas during DS, lower ALWC results in more concentrated H⁺ and hence lower pH. In fact, the pH in these two cases are the opposite trend. Specifically, the authors should provide detailed data or modeling results to validate the inferred relationship between ALWC, ionic composition, and pH, and to strengthen the mechanistic interpretation of WSOC partitioning behavior across all the measured data.
7. In Lines 249-253: How can the author determine that the coarse particles are enriched with Ca(NO₃)₂ or CaCO₃?
8. In 238-246, the role and influence of IMs for Fp of WSOC was not clear? IMs were mainly formed through the aqueous reaction of NH₃ and carbonyls. The low ALWC would not favor the formation of IMs. It should give more discussion, such as the phase state.
9. In Lines 255-258, the author pointed out that N₂O₅ hydrolysis would promote NO₃^- formation due to those mineral dust particles and hygroscopic, but in DS, no obvious NO₃ formation occurred compared other observed time. Thus, it did not support a linear correlation between NO₃^- and NH₄⁺ in the coarse mode. Please clarify it. In addition, this discussion should apply to the whole campaign, including WSOC, Fp, pH, size distribution and driving factors.
10. In Section 3.4, the author should give the detailed information of the measurement of absorption, such as the solvent, the filter mass, etc., to reduce the uncertainty. In addition, the relationship of the concentration of chromophores or the ratio to WSOC with MAC or Abs should be added to differentiate the dust and haze. The filter of dust is yellow, but the haze filter may be black or grey, how to differentiate the influence of inorganic components.
11. Check the references (pages, volume, issue, journal (abbreviation or full), etc.) to meet the requirement of ACP.
12. The current title of the manuscript is overly long and could be more concise. A shorter, more focused title would improve readability and better reflect the core content of the study.