Comments on egusphere-2026-389:

1. Samples were collected using different filters, samplers, flow rates, and protocols. Although blank correction is mentioned, please describe campaign-specific field/procedural blanks to demonstrate cross-site comparability.
2. Lines 176-186: Horseradish peroxidase assay is not specific to H₂O₂, did you ever consider organoperoxides or other oxygenated species that act as efficient electron-acceptors? The quantified H₂O₂ can only be treated as equivalent result。
3. In method section, QA/QC should be discussed or informed
4. Line 213-217: The MCR boundaries were developed primarily for CHO compounds, whereas the present study applies them to CHON, CHOS, and CHONS formulas. Please justify this extension and provide a CHO-only or formula-class sensitivity analysis.
5. Lines 372-382: This interpretation is overstated. ROS-forming efficiency depends on composition, medium, pH, and assay endpoint. The present results represent water-extractable H₂O₂/radical yields, not general “intrinsic ROS activity.” Tong et al. (2018) demonstrated medium-dependent (water vs. surrogate lung fluid) ROS yields for naphthalene SOA, while Li et al. (2022) showed strong pH effects on the peroxide content and oxidative potential of biomass-burning HULIS. Aqueous ROS yields also should not be extrapolated directly to cellular ROS responses. Please qualify this conclusion throughout the manuscript.
6. Line 459: Replace “higher intrinsic reactivity” with “greater aqueous ROS-forming potential under the present assay conditions.”
7. Several key correlations are based on only five or six averaged observations. Please report sample sizes, regression statistics, confidence intervals, and individual data where possible, and moderate claims such as “robust predictor” and “fundamental compositional control.”
8. LC-ESI-MS peak-area fractions are signal-weighted rather than quantitative mass or molar fractions because ionization efficiencies vary among compounds. Please revise the terminology and acknowledge this limitation.

Minor corrections:

1. Line 122: correct to “field campaigns”
2. Line 145: delete repeated “while”
3. Line 275: change “MR-VK” to “MCR-VK”
4. Line 393: change “Figures 4” to “Figure 4”

This manuscript investigates the relationship between the molecular composition of organic aerosol (OA) and reactive oxygen species (ROS) formation using an MCR-VK framework. The authors combine ultrahigh-resolution mass spectrometry with ROS measurements across a wide range of ambient environments, including several Chinese megacities, a semi-urban site in Germany, a boreal forest site, and laboratory-generated SOA. The combination of field observations and laboratory experiments is a major strength. I find the manuscript generally well organized and scientifically interesting. The manuscript is potentially suitable for publication in Atmospheric Chemistry and Physics after revision. I have several comments that I believe could further strengthen the manuscript and clarify the interpretation of the results.

1. One point that I think deserves some clarification is the use of RFOOC/RFUOC as an indicator of aerosol oxidative activity. As I understand it, these values are calculated from the relative LC-MS peak areas. Because different compounds can have very different ionization efficiencies in ESI, the peak-area fraction does not necessarily correspond to the actual abundance or mass fraction of OOC and UOC. I think this limitation should be stated more clearly.
2. The OOC category appears to include a chemically diverse group of compounds. Some highly oxygenated compounds may be efficient ROS precursors, whereas others may not be particularly reactive. Therefore, it is worth emphasizing that OOC is a molecular-composition descriptor rather than a homogeneous group of ROS-active compounds. This would make the mechanistic interpretation of the results more balanced.
3. Lines 270-272: I don’t think HOMs/Aromatics can really be considered independent validations. Both HOMs/aromatics and the MCR-VK classification are derived from the same UHRMS molecular-formula data. I suggest replacing “independent structural indicators” with something like “complementary molecular indicators” or otherwise clarifying this point.
4. Lines 396-402: regarding the exponential relationship in Figure 4a, I am not sure that the fitted relationship alone is sufficient to support the saturation behavior. The nonlinear relationship is interesting, but the saturation could simply describe the empirical distribution of the data. I suggest either providing additional evidence for the proposed mechanism or making this interpretation more tentative.
5. Lines 505-510: While the authors acknowledge the potential role of transition metals in ROS formation, it should also be emphasized that the current analysis does not quantitatively separate the contribution of OA from that of inorganic components.

Minor comment:

1. There appears to be a wording error in line 145: “while it was while 0.5–1 ppm for isoprene and naphthalene.”
2. Lines 415-419: Mismatch between the text and Figure S7; I actually think this discussion can be deleted.
3. Line 195: Provide references to support the statement that short-lived radicals are “assumed to rapidly react with BMPO”.
4. Line 492: The statement that the MCR-VK framework is “broadly applicable to chemically diverse atmospheric aerosols” seems somewhat stronger than supported by the current dataset, particularly given the deviation of Hyytiälä from the urban relationship. I suggest softening this statement.
5. Line 494: There is an extra period in “oxidative activity..”
6. Line 499: Replace “further validates these conclusions” with something slightly more cautious, such as “provides further support for these conclusions.”