General Comments

This study reports the characterization of organosulfates (OSs) in PM2.5 samples collected from three urban sites using UHPLC-HRMS to obtain molecular composition data to perform precursor-constrained PMF source apportionment and OSs–precursor correlation analysis for classification of detected OSs. While this study presents a lot of data, it remains unclear to me how precursor-constrained PMF source apportionment was performed in this study using molecular composition data from UHPLC-HRMS. Specifically, I did not find details about how the source profiles were established and the critical QA/QC elements (e.g., the residual matrix, Q value, and related diagnostics) for validating the statistical robustness and chemical realism of the results. The testing variables and correlation analysis results were not presented in a clear manner, making it difficult to assess the validity of the findings. Substantial revisions and further clarifications are required to help the readers better understand the reported data and its implications.

Specific Comments

Lines 92-97: Can the authors provide some scientific rationales for why these three sampling sites were selected? Do they have distinct emission sources or meteorological conditions that can be tested as variables?

Lines 111-114: Did the authors have estimates for the extraction efficiencies of OSs from filters using this protocol? This information is critical to assess analytical uncertainties and validate quantification.

Lines 138-143: Can the authors provide some context about what “Xc” means and how this value can aid in the identification of OSs?

Line 151: Can the authors provide more detailed information about what “conventional classification approach” means and specify how it is different from the current precursor-constrained PMF source apportionment?

Line 176: Can the authors explain why isoprene VOC markers were included, given that only OSs with C ≥ 8 were analyzed?

Lines 180-185: For the calculated correlation coefficients, I have a few questions about this section.

• How were the VOCs collected and analyzed at the sampling site? Were they measured in real time?
• How were the correlations between classified OSs/NOSs and corresponding VOCs calculated if data were not collected and analyzed at the same time resolution?
• How did the authors confirm that the measured isoprene emissions were from biogenic sources in winter at the sampling sites, given that isoprene is primarily emitted from deciduous plants?

Lines 238-248: This paragraph is confusing, and the statement seems contradictory. Can the author clarify how relatively low anthropogenic emissions and low RH promote the dominance of Aliphatic OSs and NOSs, since the precursors for Aliphatic OSs and NOSs (e.g., long-chain alkenes) were also from anthropogenic emissions?

Lines 249-252 (Figure 2): The authors should provide more details about how “classification” was performed.

Line 254: The conventional classification approach should refer to Figure 2(a).

Lines 309-318: This discussion seems mostly speculative. Can the author provide more definitive evidence about how oxidation of long-chain alkenes can potentially form cyclic intermediates that can undergo acid-catalyzed ring-opening pathways for Aliphatic OSs and NOSs formation?

Line 333: What do the “public molecular composition datasets” refer to here?

This manuscript presents a valuable study on organosulfates (OSs) in PM2.5, combining molecular-level characterization, source apportionment, and OS–precursor correlation to improve OS classification in urban aerosols. The results reveal previously underestimated contributions of aliphatic OSs and nitrooxy OSs (NOSs) and highlight key formation factors such as aerosol liquid water content, inorganic sulfate, Ox, and pH. The study is scientifically sound and provides important insights into urban SOA formation. However, some methodological details (e.g., filter baking, extraction procedure, instrument calibration, and polyisotopic ion identification) require clarification to ensure reproducibility. After addressing these points, the manuscript would make a significant contribution to the field.

Specific Comments

1. Line 98 – The filters were generally baked at 550 ℃ before collection. Did the authors perform this step? This should be clarified.
2. Lines 112–114 – How many extraction cycles were conducted, and what volume of methanol was used? What were the extraction efficiencies of OSs from the filters? More detailed information about the extraction procedure would be helpful since OSs were quantitatively analyzed.
3. Line 115 – Did the authors calibrate the instruments used in this study?
4. Line 135 – Polyisotopic ions must be identified during molecular formula assignment to avoid misinterpretation of molecular compositions. It appears that the authors may not have performed this step.
5. Lines 194–200 – Were there any sulfur-containing compounds that could not be assigned? How did the authors calculate the total mass concentration of OSs?
6. Line 209 – ALWC indeed plays an important role in OS formation. However, ALWC is also influenced by temperature and aerosol hygroscopicity in addition to relative humidity. Could the authors provide the specific ALWC values here? This would help readers better follow the discussion.
7. Lines 213–215 – How did the authors determine this?
8. Lines 218–219 – The authors emphasize a new classification approach here and in the Introduction. However, this approach does not appear to show clear distinctions compared with previous methods. More detailed description of the current approach should be provided in the revised manuscript.
9. Line 221 – Each numerical value shown here should correspond to the respective city.

This study by Qiu et al. investigates organosulfates in aerosols in three Chinese megacities, Beijing, Taiyuan, and Changsha, using an integrated framework that combines LC-Orbitrap mass spectrometry with non-targeted analysis. Additionally, precursor-constrained PMF analysis, together with meteorological data (RH, ALWC, sulfate, Ox), were incorporated to provide a detailed interpretation of the formation pathways. It is interesting that the authors installed a denuder upstream of the sampler to remove SO₂ during sampling, which helps demonstrate that the detected organosulfates are not solely sampling artifacts, a concern raised in previous studies. The novel integration of nontarget analysis of HPLC-Orbitrap mass spectrometry data with precursor-constrained PMF offers an alternative and informative approach for classifying organosulfates from a molecular perspective, representing a valuable methodological contribution to the field. Overall, the manuscript is well written and well structured, however there are several grammatical errors which should be corrected. The comments below should be carefully addressed before the manuscript can be fully considered for publication in Atmospheric Chemistry and Physics.

General comments:

1. Sampling was conducted only from December 2023 to January 2024. However, organosulfate formation is highly seasonal, particularly for pathways driven by biogenic emissions and photochemistry. The authors should discuss that the results may not represent annual OS behaviour.
2. The precursor-constrained PMF uses only a limited set of VOCs. which is reasonable. However, many OSs come from multiple or unknown precursors, so the source assignments may not be very stable. The authors should discuss how VOC correlations might affect the results and the possibility of misclassification.
3. Discussions of formation pathways mainly rely on correlations with RH, ALWC, sulfate, and Ox. While these correlations are informative, they do not establish mechanistic causality. Strong statements about OSs formation (e.g., heterogeneous formation, as noted throughout the manuscript) would be better presented as hypotheses supported by observational evidence, rather than as definitive mechanisms.
4. This work quantifies organosulfates using a few surrogate standards. Table 1 lists four standards, but it is stated that only compounds with more than 8 carbon atoms are quantified, thus one standard is excluded. However, as reported by e.g. Ma et al. 2025, Nat. Commun., the structural diversity of organosulfates leads to varying ionization efficiencies, introducing significant uncertainty in absolute concentrations. A more detailed discussion of these uncertainties is needed to strengthen the quantitative interpretation.
5. More details should be included in the experimental section. This includes e.g. aerosol collection (type, flow rate) and the denuder (including efficiency in removal of SO₂).

Specific comments:

In the title “Revealing the” could be removed.

L22: “Organosulfates (OSs) are important component of” -> components. You define OSs as the plural of organosulfates, however in many instances it is better to use the singular e.g. line 27 OS precursor. This is often the case when OS is part of a composed wording (such as this example).

L24. It is not clear to the reader what you mean by “classification” here.

L28. Please add “China” after the list of cities.

L39. What do you mean by “indicative role”?

L55: vital seems like a strange word here.

L64. This seems like a very strong statement given the uncertainties of the current approach.

L75-76: “For instance, increased aerosol liquid water content (ALWC) enhances OSs formation by promoting the uptake of gaseous precursors (Edwards et al., 2017; Brown et al., 2012)”. Both papers report on NOx so it is not clear how they support this statement.

L82 NTA is already defined.

L84. State that the cities are in China.

L93: Could the authors provide more information on why they conducted their research in these three cities? Can the authors discuss the extent to which organosulfate formation mechanisms can (or cannot) be generalized across different locations?

L108: This was probably not 40 days for all filters? What is the reason for 24 h equilibration of filters, with potential for artefact formation?

L112: Please make sure to be specific so you need to state that extracts (not filters) were filtered.

L114: Why are the samples redissolved in pure methanol? This could be the cause of the issue with analysis of early-eluting compounds. Please comment on this.

L135-136: s = 0-1!

L144-145: Organosulfates primarily fragment under MS² to produce ions would be HSO₄⁻ and SO₄^•− whereas HSO₃⁻ and SO₃^•− are characteristic of organosulfonates.

L147: Although nitrooxy-organosulfates contain nitrogen, they are still a subtype of organosulfates. Since the authors discuss them together throughout the manuscript, it may be clearer to group both nitrooxy-organosulfates and organosulfates under the general category of “organosulfates.” This would also simplify the presentation of Figure 2.

L149: While reversed-phase columns can struggle with highly polar, very small organosulfates, I do not agree that they inherently have limitations for species as large as C7. In practice, such limitations are typically restricted to OSs with very short carbon chains (e.g., C1–C3), where retention becomes insufficient. Moreover, the authors themselves used a C6 organosulfate as a standard, which further suggests that the method is capable of measuring species in this size range. Or is this issue due to the pure methanol solvent?

L178: In some instances it is 8 groups and in others 7. Please be consistent.

L183-184: This sentence needs clarification.

L196: Give the variation, one decimal is more appropriate here.

L212-217: This section is quite speculative, which should be better reflected in the text. The time series of metals from fireworks show shorter spikes in concentrations, while sulfate and organosulfate concentrations are elevated for longer periods. K can also stem from biomass combustion.

L219: It is not clear what you mean by “conventional”. Please be specific.

L237: What is the standard deviation of this number?

L245. It seems unclear why low anthropogenic emissions would promote dominance of aliphatic OSs and NOs. Please clarify or correct.

L254: Figure 2(a)?

L269. Please provide some suggestions or hypotheses.

L288:  I did not find data point below pH 1.0.

Figure 1:

(1) Please increase the resolution of the figure for better clarity.

(2) As the authors argue that increases in ALWC facilitate OS formation through aqueous-phase reactions, could you also discuss why the 31 December sample from Beijing showed the highest organosulfate concentrations despite having low ALWC?

(3) Please consider replotting the RH data. Currently, a color gradient is used to represent different RH values for each day, but the points are connected with lines that retain the previous point’s color. This presentation is somewhat confusing, as it may give the impression that RH remained constant over several days, which is not the case.

(4) Please state clearly in the figure text that the time scales are different between sites.

Figure 2:

Please increase the resolution of the figure for better clarity.

Figure 3:

The color scheme in panels (a) and (b) should be improved, as some colors, particularly the light yellow, are difficult to distinguish.

Please explain in the figure text that the grey dots are Aliphatic OSs and NOs.