This paper uses filter samples collected at a number of sites in Switzerland over a period of roughly a year to determine particle oxidative potential by three methods for PM2.5 and PM10.  The paper adds to a growing list of research that assumes OP is a relevant metric to relate aerosol chemical properties to adverse effects on human health, although they present no data on this in this paper.  The paper investigates what sources contribute most to the measured OP and claim to investigate what the chemical components are that drive it (objective (ii) line 90). They also assess the performance of the assays, concluding that one of them is a more specific metric, which is interpreted, I guess, to mean a better connection to human health (more on this below)?  The paper essentially reinforces the view that with declining vehicle tail pipe emissions, the two main emission sources of concern are particles emitted from vehicle brakes and abrasion of tires and roadways and wood burning (residential). The paper, however, does not really address what specific compounds drive the OP since they do not sufficiently chemically speciate the OA (they only find traces of wood burning linked to OP (i.e., sugars), which are likely only markers, and they do not actually measure metal ions which are the species that would be driving the OP assays. (For example, the lines 370-374 really apply to all the specific PM components measured, including the metals).  The paper is well written and the data is interesting. However, there are areas where the authors could provide more clarity, but overall, it is an important contribution.

Detailed Comments:

Simple linear models involving various species are used to reconstruct the observed OP levels, and they seem to do a reasonable job given the high r2. However, other research has shown that OP measured in a filter extract is not likely simply due to the sum of individual species, there can be interaction between species.  Why does this appear not to be an issue in this data set?

Few details are given on the assays.  I think it would be useful at a minimum to note what the filter extraction liquid was for each assay (it was not water, simulated lung fluid for DTT and AA, but not DCFH?) and why was this done, e.g., Calas et al. 2017 does not appear to show a difference in ambient samples for the OP_DTT assay in pure water vs. SLF, so what is the justification?  It would be useful to explain and support why this is claimed to be important given that the authors make the point many times that lack of standard methods impedes this area of research. Also, how is the DCFH assay used so that the results are reported in units similar to the other two assays (ie, doe DCFH assay really have units of nmol/min/m3, last line of section 2.3.1.)– this does not seem possible?  And finally, the authors state that a liquid concentration of roughly 25 ug/L was used for the OP tests, but in their methods cited (Calas et al., 20218), a concentration of 10 ug/mL was used instead, a huge difference (ug/L vs ug/mL)?

Relating to the above, what does “All extracts were conducted at iso- and low-mass PM concentration…” mean.  (What is the meaning of iso-…?)

Line 375 to 380 relating to the inclusion of ammonium nitrate in the models.  The reason could be more complex than what is stated, e.g., ammonium nitrate could largely control particle water, which in turn controls aqueous reactions that affect OP, or ammonium nitrate could just be a tracer for secondary processes in general or more photochemically aged aerosol, which has been shown to affect metals solubility and OP (eg, Wong et al, Environ. Sci. Technol. 2020, 54, 7088−7096; Antinolo, et al.,2015, Nature Comm, 6(6812 ), 1-7; Li et al, 2013 Atmos. Env., 81, 68-75; Zhu et al, 2020, Envir. Sci Technol., 54, 8558-8567, and others on formation of secondary OP species) The point is, atmospheric aging alters aerosol particle chemical properties. When interpreting their data, the view by the authors seems to be that almost everything as primary.

Finally, in the Abstract and at the end of the paper it is stated that AA may be a more specific metric for OP than the other assays. This is apparently based on the idea discussed starting on line 362; that the linear models for predicting OP_AA at the various measurements sites have a wider range of tracers in them, but they still all point to the same source, brakes/road dust and wood burning. What does that mean; that AA really is only influenced be species from these two sources, whereas the other assays are also sensitive to other species that may not be from these sources? One could interpret this as; the AA assay is sensitive to fewer sources for OP (not a good thing), or that it does not include influences from species that have no effect on OP (that would be a good thing)? How do the authors even know how to decide this so as to determine what is the better assay, there is no evidence shown that these are the only main sources that produce adverse health effects under the oxidative stress paradigm (there is no health data presented in this paper)?  One may argue the opposite, that actually an OP assay that is more comprehensive, that includes more sources that can contribute to oxidative stress, is ideal.  Note, DTT included NH4HO3, but AA did not, and see comments above on this. The discussion (or argument) on the relative merits of these three assays based on the findings of this study should be discussed more thoroughly. The current logic for the assessment of these assays is not clear to me.

Grange et al. investigated the oxidative potential (OP) of ambient PM₁₀ and PM_2.5 at five sites located in different environments of Switzerland. OP was assessed using three different endpoints - ascorbic acid (AA) and dithiothreitol (DTT) consumption, and dichlorofluorescein (DCFH) assay. They explored the spatiotemporal variability of OP and compared the OP levels with those measured in France. The source analysis followed by the investigation of sensitive components were then conducted among measured PM species, mass, and OP, and the finding suggests a higher level of OPm associated with non-exhaust traffic emissions and wood burning.

Overall, this paper provides a thorough analysis of OP levels in Switzerland and its comparison with France. The selection of sites covered common types of geographical locations with high population, and the comparison of OP with those in France provided a wider spatial scope of the health effects of PM₁₀ in Europe. The results of sources with high OPm potency identified in this paper were generally consistent with previous studies in different regions, and the results pointed towards the importance of controlling local traffic emissions and woodburning. However, the protocol of sensitive chemical identification seemed to be flawed. By filtering the species with multicollinearity, some important contributing species might be also filtered. The regressions with significant R² did not present the important contributors, which might indicate the lack of scientific implications of the results from this method. Furthermore, the species that were found to be highly correlated with OP in the multiple linear regression were not critical and could be easily replaced by other species, further pointed out the weakness of this method. Therefore, I would like to recommend that the paper should be majorly revised majorly for further consideration.

Specific comments are listed below.

Major comments:

1. The materials and methods section written in the paper were too concise. The characteristics of five sampling sites, the list of measured chemical species on filters, selection criteria applied in random forest, and the factors used in PMF are not provided, and should be further described to provide a full understanding of all the protocols.
2. The level of PM used in this study (25 μg/L, i.e. 0.025 μg/mL) is far lower than that applied in most other studies (10-50 μg/mL). I highly doubt that this level may generate valid OP results. Please check the unit of the concentrations.
3. While explaining that AA is a major constituent of lung lining fluid, the paper used an AA-only model for monitoring the consumption of AA, but many studies used the endpoint of AA in surrogate lung lining fluid to better represent the biological environment in human. Please provide a justification of using the AA-only model.
4. Figure 2 combining all three endpoints in the same box seems to be confusing. Since the comparison among these endpoints is not reasonable, I would suggest splitting them into different boxes as per different endpoints, for presenting the data.
5. Grange et al. 2021 is not available online and it seems to contain a lot of information for the interpretation of this paper.
6. In lines 218-221, the authors explained the trend of OPcoarse, but this term is not well defined or calculated anywhere in the entire manuscript. Therefore, I suggest to provide further description, trend and calculation of this term.
7. The discussion of PMF results lacks depth. Even if most of the results might have been provided in Grange et al. (2021) which is not accessible now, the discussion for the MLR analysis between OP and PM sources should be enhanced. The contribution of sources towards different OP endpoints in OPv should be involved in this section.
8. The method of random forest is very ambiguous: the selection of importance based on ranking should be provided in the paper. Also, in Figure 6, the justifying criteria “ranking highly” should be quantified.
9. The results showing interchangeable species for the significant correlations between PM OP and concentration of components is concerning: the actual contributing species might be omitted during the selection and the final results could only find out the indicators towards important sources. Although some key contributing species like Cu and Mn were identified, they were eclipsed in the numerous correlation pairs of non-contributing sources and OP. This is further demonstrated by Figure 7: the pairs of species involving most significant correlations (Sb and galactosan) were not contributing to PM OP. Therefore, the causality is not indicated by this method. This should be included in the discussion of the limitations.
10. Including PM mass in the regression might not be a good idea: PM mass might have a much higher weight than the chemical species included in the model. Therefore, the results might be biased, since OPv is determined by PM2.5 mass to some extent. Therefore, I would suggest removing PM mass for the MLR analysis between OP and species.

Minor comments:

1. The introduction section should be supported by more literature. For example, in line 66-67, the statement of the different spatiotemporal trends of OP and PM mass could be supported by Yang et al. (2015) (DOI: 10.1016/j.atmosenv.2014.11.053), Liu et al. (2018) (DOI: 10.1016/j.envpol.2018.01.116) and Yu et al. (2021) (DOI: 10.5194/acp-21-16363-2021).
2. Line 37: remove “say,” .
3. Please provide further details of DCFH assay, including the cells used for this assay and assay protocols.
4. Line 148: Please provide the supporting citations for the statement “DCFH assay is sensitive to organic compounds”.
5. Line 158: Provide the full name of “SOURCES”. Also, this sentence is highly confusing: is PMF informatively known as extended PMF, or is SOURCES program informatively known as extended PMF? Think restructuring this sentence.
6. Line 220: Saying that OPcoarse is biological relevant is not rigorous since the biological relevance should not only consider the level of OP but also include the accessibility of these coarse particles in the respiratory tract. Suggest revising this statement.
7. Line 237: The comparison did not involve OP^DCFH This information should be listed.
8. Line 252: This sentence should be moved to the discussion of OP^AA in the previous paragraph.
9. Line 386: Provide the comparison of numbers of pairwise combinations between PM₅ and PM₁₀.

general comments:

Grange et la. presented three OP measurements at five different sites in Switzerland. Spatial and seasonal variations are discussed. A MLR model was then used to link OP to PM sources resolved with PMF and the results suggest that road traffic and wood combustion are the major sources. Lastly, the authors used a machine learning algorithm to identify the most important PM constituents to explain OP-DTT and OP-AA to be non-exhaust metals and wood burning organic tracers. Overall, the work is interesting while more details and explanations are needed. I recommend acceptance with some minor revisions.

specific comments

1. line 129, the consumption of AA could also be due to direct reactions between PM components with AA for example metals.
2. section 2.5, it is still not clear how OP are linked to PM sources identified from PMF using MLR. More details are needed. What are the results for slope coefficients? Are the model interpretation based on the assumption that the sources contribute linearly to OP? How was OPm calculated? OP was not included in the PMF models. Won’t it be more reasonable to just include OP in the PMF model? It would also be helpful to see if including OP in the model result in a better representation of OP-DCFH.
3. Rubidium seems to rank top 4 in all cases. This has never been found in any other previous studies, to my best knowledge. Is Rubidium DTT- and AA-active or is it linked to OP sources? What are the sources of Rubidium in Switzeland? Please provide references that indicate rubidium as a tracer for wood burning.
4. Figure 5, the color points are quite scattered, however, no discussion on uncertainties at all.
5. line 218, PM-coarse contained much of OP signal, it would be helpful to provide numbers, ie. % of PM-coarse in total PM
6. line 223, “lower levels of structure” is confusing. do you mean low levels of spatial and seasonal variation?

technical corrections

1. line 120, typo in 25 ug L-1? Should be ug mL-1 instead?
2. line 273, typo in DFCH