The authors Li et al describe a series of analyses on the oxidative potential (OP) and molecular composition of filter-collected ambient particles as well as the inter-relation between these two measured qualities. The experiments are well executed and provide interesting insights on both ambient organic aerosol (OA) composition as well as the compounds affecting OP within OA and the results will be useful in informing how we understand the health effects of ambient aerosol. I have several comments on the methodologies employed and some of the conclusions drawn, but I believe that after these comments are addressed the manuscript will likely be suitable for publication.

Section 2.2:

Why were different solvent conditions (methanol vs ACN) used for WSOM samples that were directly analyzed by FT-ICR MS and those that were first derivatized? Additionally, prior work (e.g., Chen et al., 2022) has observed methanol (but not ACN) extraction to induce chemical reaction in some carbonyl-containing molecules; in the work of Chen et al., this was observed for the carbonyl-containing molecules phthalic and maleic anhydride. The full impacts of methanol-induced reactions during extraction in the present work is not immediately clear to me, but this possibility should be discussed. 

Can the authors comment on the expected efficiency of the carbonyl-PFBHA reaction? From a quick look through the literature the extent of reaction seems to have some variability across different reactants and conditions. I realize that myriad molecules make up OA/WSOM and an evaluation of all is impossible, but some discussion or analysis of the expected extent of reaction with a small subset (for example, carbonyl molecules identified in prior work as contributing to OP, lines 251-254) would be useful.

Section 2.3

To what extent does the upper limit of the mass range impact the analysis? For example, a molecule with one carbonyl group and exact mass > ~725 would be detected in the non-derivatized sample but the derivatized analyte would be above the mass range and not detected, potentially leading to undercounting the number of carbonyl molecules and affecting the quantities reported in Figure 1 and the associated discussion on molecular characteristics. Relatedly, what proportion of detected carbonyls are singly vs doubly vs triply derivatized? My understanding is that it's not uncommon for molecular components of OA to contain multiple carbonyl groups, particularly molecules derived from aromatic-containing precursors, and it appears that such molecules may only be detected (as carbonyl-containing) when the underivatized molecule is relatively much smaller than many other analytes.

Is the automatic screening procedure referenced from Yu et al. (2023a) also described in a peer-reviewed publication? If so, please reference it here, and if not, please add more detail to the current manuscript.

Section 3

Lines 205-206: I believe more context is needed around the seven categories overlayed on the Van Krevelen diagrams. These categories were originally developed following analysis of dissolved organic matter rather than OA, so the delineations most relevant for DOM may not be the most useful for OA, with its own unique combination of primary and secondary organic molecules. A discussion of the category definitions and molecular characteristics would provide more clarity to the aerosol community. 

Lines 248-251: It's not clear to me from the text and axis labels in Figure 2c,d whether the "abundance" of carbonyl molecules used for correlation analysis is just the number of carbonyl molecules (as implied from the labels in Figure 2c,d) or an abundance where each carbonyl signal is weighted by its signal intensity (which may make more sense).

Lines 251-254: what molecular categories would the three sets of molecules described here from prior work be classified into if they were in Figure 1a? For me, the text here led to some dissonance with the categories used in Figure 1a; for example, I know 1,4-benzoquinone (a quinone) is an unsaturated hydrocarbon, but based on O/C and H/C it would be considered aromatic. Similarly, molecules from Han et al. (2020) are described as "unsaturated," which is true, but these naphthalene-derivatives do not appear as though they would fall into the "unsaturated hydrocarbons" category of Figure 1. Please add additional context to the descriptions of molecules from prior work in relation to how chemical structures are categorized in this work.

Line 266: Might NaBH4 treatment induce any other reactions? If so, please note here, as well as whether these reactions likely have relevance to molecular structures in atmospheric OA.

Line 268: Were ambient-collected OA samples not available for this analysis? My recollection is that SRNOM has some similarities to OA from biomass burning and cloud-water samples but is not a perfect analogue.

Line 275: would some amount of non-removal be expected in this type of analysis? Does this indicate anything about those unreacted molecular structures?

Lines 320-321: the concluding sentence to this paragraph needs additional context. I would agree that the results here suggest aromatic-derived carbonyl molecules merit further attention, but there are a very low number of carbonyl-containing molecules in the "aromatic molecules" category on the VK diagram according to the data presented in Figures S8 and S9. However, the lignin-like and tannins-like categories are also defined around structures that contain aromatic rings, among other functionalities, and would likely have high AI and DBE values as well. Please clarify and update the text accordingly.

Lines 328-329: I'm not certain that the analysis presented in Figure 5b is entirely appropriate. The compound spaces defined in Kroll et al. (2011) and represented by the shaded spaces are derived from AMS measurements and volatility-based estimations of #C. As noted in Kroll et al., AMS measurements are imperfect due to the substantial fragmentation that occurs during analysis, leading to the loss of most detailed molecular information. Given the substantial differences in analytical techniques between this prior work and the current MS measurements that provide molecular formula with high accuracy, I'm not certain that a direct comparison in this manner is appropriate. Additionally, the O/C:#C space categories detailed in Kroll et al. are not exhaustive (as AMS measurements have advanced considerably in the years since) and do not include some aerosol types that may be relevant for this work, such as aged biomass OA, primary/fresh or secondary/aged OA from combustion related to residential heating, or cooking OA. 

Line 339: can the authors be more specific regarding "combustion by-products?" Combustion can cover a variety of activities with different emissions profiles, including combustion related to vehicles, industry, power generation, or heating.

Section 4

Lines 356-368: The discussion in this paragraph feels odd, given that the first sentence highlights the importance of aromatic carbonyl molecules for OP and the rest of the paragraph focuses on the reactions of non-aromatic carbonyls that, as best I can tell, do not contribute strongly to OP; consider revising. The oligomerization reactions highlighted here tend to produce molecules with high O:C ratio and a range of H:C ratios, depending on the reactions, that would appear to place these products mostly in the tannins and carbohydrates categories on the VK diagram. The authors observe plenty of carbonyls in these categories (Figure 1a) but almost none that are strongly associated with OP (Figure 5a), which I suggest the authors also discuss.

Lines 372-373: is the statement that "no significant decrease in atmospheric carbonyls during the Winter Olympics was observed" based on the number of unique carbonyl molecules observed or the absolute signal apportioned to carbonyl molecules? Based on the large drop in OA mass between the winter and Winter Olympics periods I would be surprised if the amount of carbonyl molecules within OA remained constant.

Lines 373-375: I agree with this statement, but it also seems to me that, based on my understanding of the data, the authors can give more detail on likely sources of carbonyl-derived OP in the collected aerosol samples. The authors demonstrate a link between OP and carbonyl molecules with aromatic content (based on AI and DBE) and show a lack of decrease in OP following emissions reduction during the Winter Olympics when traditional OA sources such as industry and transport decreased but other sources like heating (or potentially cooking?) did not. To me, this suggests that combustion related to residential heating may be a significant source of carbonyl molecules that contribute to OP, as the authors mention at Line 240, and that changes to residential heating techniques or air quality may reduce the OP of OA. Are there previous studies that examine changes in air quality and OA composition during the Winter Olympics period that might inform the authors' discussion on OP during the winter and Winter Olympic periods?

Technical comments: I suggest removing instances of informal language in the Introduction (e.g., "more and more," "tip of the iceberg,"). I also suggest adding a more complete description of the word "montane," as this word is not commonly used and may be unfamiliar to some readers.

References

Chen, K., Raeofy, N., Lum, M., Mayorga, R., Woods, M., Bahreini, R., Zhang, H., & Lin, Y.-H. (2022). Solvent effects on chemical composition and optical properties of extracted secondary brown carbon constituents. Aerosol Science and Technology, 56(10), 917–930. https://doi.org/10.1080/02786826.2022.2100734

Li et al., utilized FT-ICRMS technology with their established screening procedure enabling a high-throughput screening of carbonyl molecules in ambient aerosol samples. They further linked these data with the DTT activity of water-soluble organic matter and found a positive correlation between carbonyl molecules and DTT activity. By employing several statistical tests and modeling, they proposed oxidized aromatic compounds containing the carbonyl group could be used as potential markers of atmospheric oxidative stress. Overall, I think these data are beneficial and the results are of great importance. I would recommend publication after the following concerns are addressed.

1. A significant correlation between DTT_OC and the number of carbonyl molecules was observed; however, the molecular intensity of carbonyls was not taken into account. I suggest the authors should consider weighing the effects of intensity and examine how it may affect the correlation.
2. The authors utilized Suwannee River natural organic matter and diesel soot to validate a decrease in DTT activity after the removal of carbonyls. I suggest the authors should discuss why similar experiments were not performed using real ambient WSOM. If feasible, conducting additional experiments to demonstrate a substantial decrease in DTT activity after removing carbonyls for ambient WSOM is recommended. Such results would enhance the credibility of the findings. At the very least, the representatives of Suwannee River natural organic matter and diesel soot should be discussed in the manuscript.
3. The reported DTTm (Figure 2) is over an order of magnitude lower than the general reported DTTm in literature (e.g., Yu et al., Journal of Hazardous Materials, 2022 (10.1016/j.jhazmat.2022.128839); Campbell et al., Atmos. Chem. Phys., 2021 (10.5194/acp-21-5549-2021), works for Beijing DTT activities). Please discuss the possible reasons for the difference.
4. Furthermore, based on the discrepancy between DTTv and DTTm in Figure 2, it appears that they cannot be converted by the equation provided by the author. For instance, to obtain the DTTv shown in Figure 2, the DTTm would need to be multiplied by approximately 1000 ug/m3 PM2.5 concentration. I recommend double-checking the data for accuracy. Additionally, please include the PM2.5 concentrations in Table S1, and it would be preferable to provide TOC concentration data for the air rather than in the WSOM extracts.
5. Figure S11 will be more informative by showing the categorized groups of molecular formulas for different sampling periods instead.
6. Line 244: “… This is likely due to the differences in aerosol sources in different seasons.” please expand the discussion, e.g., what could be the main sources for DTT in summer and winter, respectively.
7. Line 338: “These results suggested that aromatic secondary products containing carbonyl group produced from combustion by-products in winter are potential molecular markers of atmospheric oxidative stress.” Here I suggest the authors discuss the study by Liu et al., es&t, 2023 (10.1021/acs.est.3c03641), where similar findings are observed for cellular oxidative stress. Also, the authors should clarify the combustion activities only occurred in winter (and also during the winter Olympic period) but not in summer.
8. Conclusion section: the first paragraph regarding the authors’ FT-ICR-MS method was not discussed in the Results and Discussion section and is not rational to be a conclusion of this work.
9. Conclusion section: aromatic carbonyl molecules are suggested as indicators of atmospheric oxidative stress. However, the second paragraph primarily discusses the possible formation sources of general carbonyl molecules, such as terpene and isoprene oxidation, which do not produce aromatic carbonyl molecules. The authors should revise the discussion to be more explicit and focused. Otherwise, the current discussion on the formation pathways of carbonyls seems to favor summer conditions, which contradicts the findings of this study.

Minor comments:

1. In Figure S2 (a) and (b), the fittings for blank samples look incorrect. The fitting curves do not come across any data point.
2. Please clarify the sampling period for each sample. Was it 24-hr sampling?
3. A number of typos in the manuscript, please carefully check. E.g., WSOM has been written as WOSM here and there.
4. Figure S11, “CHO” figure, x-axis, “oC=O” should be “”no C=O