The manuscript from Barbero et al discusses the development of a new automated instrument to measure oxidative potential (OP) of ambient particles, using two assays – dithiothreitol (DTT) and ascorbic acid (AA). The OP of the particles is a novel property of the ambient particulate matter which has gained a lot of attention due to two reasons – 1. mechanistically it seems to be more closely related with health effects of the particles given high reactivity of ROS and the chemical components which show higher reactivity towards the generation of ROS; 2. The epidemiological studies which show better correlation of OP with specific clinical endpoints. However, the uptake of OP data in the epidemiological studies is somewhat limited due to more rigorous protocol of OP measurements than other properties of the PM. The traditional methods of measuring OP also suffer from limitations such as not being able to capture the effects of semivolatile and unstable species. The field of OP measurement is rapidly changing with newer methods and instruments being developed in the recent decade. Therefore, this paper discussing the development of a new OP instrument capable of making real-time measurements is quite timely. However, there are some concerns which the authors should consider or at least discuss in their manuscript before I recommend for its publication.

General comments:

1. This manuscript uses a standard and commercially available device to collect the ambient PM in suspension. The device operates at a fixed sampling flow rate, which is generally low (10.5). Given this, the instrument works great in a polluted environment where the high PM concentrations can get easily yield concentrated slurry in the biosampler. However, I am clear how the instrument will work in the clean (low pollution) environment. The authors mention that the concentration of antioxidants can be decreased to enhance the sensitivity of the OP method. However, given antioxidant oxidation rate is proportional to initial concentration, this will change the activity. In such a case, how can one compare the activity obtained from different studies?
2. How did the authors withdraw the extract from the biosampler in an automated manner? I didn’t see any description of the modification of the biosampler.

Specific comments

Line 35: The reference “State of Global Air Report” is repeated.

Line 76: “none is currently qualified for long-term automatic online measurements”. I think the instrument developed by Puthussery et al. 2018 (AMT) has been successfully deployed in several field campaign. It is surprising that the manuscript doesn’t even discuss that.

Line 106: “AA and DTT are then respectively added in each plate to initiate their oxidation by PM induced ROS”: I think the author is confused here. The oxidation of AA and DTT is initiated mostly by PM, leading to the formation of ROS. Although, the oxidation might be initiated by PM-induced ROS but to what extent is not known.

Line 147: It is a good strategy to install both temperature and humidity sensor at the inlet and outlet of the unit to assess the extent of evaporation in the biosampler. However, the question remained how you take this evaporation into account for calculating the DTT activity. As I understand, the evaporation will increase the concentration of DTT in the reaction vial. It is OK if the extent of evaporation is constant every time. However, that is not the case. So, my question is that in an automated system like this, do you have to do post-processing of the data to adjust of this evaporation effect in the DTT activity calculation? And if so, how do you do it?

Line 186: Is the slope of DTT and AA determined based on the measurements conducted only at two timepoints, i.e. t=10 and 15 minutes. Does this account for any non-linearity in case of very high DTT/AA activity?

Figure 3: Did the authors compare the results of their characterization of the biosampler with existing literature. Biosampler is a standard commercially available device and I am sure there should have been studies on characterizing its size-segregated collection efficiency.

Line 270: The oxidation of AA doesn’t involve Fenton-type radical reactions. The superoxide radicals generated following the oxidation of AA can react with Fe, which is a Fenton reaction.

Section 3.2.1: The ozone interference tests were conducted only for AA assay and not for the DTT assay, why? Also, why didn’t the authors consider using activated charcoal to remove ozone?

Figure 7: The horizontal error bars in this figure are quite large. Though, the authors mention them in the text below but what is the cause of such large uncertainty in the offline measurements.

Line 402: Use of 20 mm filter: The filter by filtration theory can affect much smaller particles than 20 mm (e.g. by diffusion). Did the authors characterize the penetration efficiency of this filter before deployment? Also, if the authors intended to remove larger particles, why didn’t they consider the use of PM10 impactor which will affect only larger particles and not smaller?

The manuscript from Barbero et al. describes a new online instrument for the measurement of the oxidative potential (OP) of air (PM+soluble gases) samples using both the ascorbic acid and dithiothreitol assays. To the reviewer’s knowledge, while there are other oxidative potential or ROS measurement instruments available, there isn’t any equivalent to the one proposed in this manuscript. The work is, therefore, undoubtedly novel. It has long been recognised that PM mass is not an adequate metric for determining health impacts, and OP has been proposed as a more useful metric. The instrument proposed here is therefore addressing a need of the air quality community.

I have a series of comments and suggestions that I would like to see addressed before final publication. They are described point-by-point below.

1. The abstract should mention the results of the comparison between the online device and the offline measurements.
2. Line 35: please fix the citation, it looks like it is repeated twice
3. Line 44: trace metals should also be mentioned as a potential cause for oxidative stress
4. Line 46: transition metals do not act only as ROS producers, they can also do redox chemistry themselves depending on their oxidation state
5. Some relevant literature on OP has been omitted in the introduction:

Campbell, S. J., Utinger, B., Barth, A., Leni, Z., Zhang, Z.-H., Resch, J., Li, K., Steimer, S. S., Banach, C., Gfeller, B., Wragg, F. P. H., Westwood, J., Wolfer, K., Bukowiecki, N., Ihalainen, M., Yli-Pirilä, P., Somero, M., Kortelainen, M., Louhisalmi, J., … Kalberer, M. (2025). Short-lived reactive components substantially contribute to particulate matter oxidative potential. Science Advances, 11(12), 8100. https://doi.org/10.1126/sciadv.adp8100

Shahpoury, P., Harner, T., Lammel, G., Lelieveld, S., Tong, H., & Wilson, J. (2019). Development of an antioxidant assay to study oxidative potential of airborne particulate matter. Atmospheric Measurement Techniques, 12(12), 6529–6539. https://doi.org/10.5194/amt-12-6529-2019

Shahpoury, P., Lelieveld, S., Johannessen, C., Berkemeier, T., Celo, V., Dabek-Zlotorzynska, E., Harner, T., Lammel, G., & Nenes, A. (2024). Influence of aerosol acidity and organic ligands on transition metal solubility and oxidative potential of fine particulate matter in urban environments. Science of the Total Environment, 906(August 2023), 167405. https://doi.org/10.1016/j.scitotenv.2023.167405

Shahpoury, P., Lelieveld, S., Srivastava, D., Baccarini, A., Mastin, J., Berkemeier, T., Celo, V., Dabek-Zlotorzynska, E., Harner, T., Lammel, G., & Nenes, A. (2024). Seasonal Changes in the Oxidative Potential of Urban Air Pollutants: The Influence of Emission Sources and Proton- and Ligand-Mediated Dissolution of Transition Metals. ACS ES&T Air. https://doi.org/10.1021/acsestair.4c00093

Shahpoury, P., Zhang, Z. W., Arangio, A., Celo, V., Dabek-Zlotorzynska, E., Harner, T., & Nenes, A. (2021). The influence of chemical composition, aerosol acidity, and metal dissolution on the oxidative potential of fine particulate matter and redox potential of the lung lining fluid. Environment International, 148, 106343. https://doi.org/10.1016/j.envint.2020.106343

1. In the paragraph starting at line 68, it would appear that the methods developed by Wragg, Campbell and Utinger are semi-automatic but they have been deployed for online/real-time measurements.
2. Line 73, the prototypes by Campbell and Utinger do not combine two assays in one instrument, they are actually two different instruments: one for ascorbic acid and one for DCFH.
3. Line 105, what filters have been used, and what was the extraction procedure?
4. Please discuss possible interferences from brown carbon in the absorbance measurements.
5. Line 141, please provide details of the filters used in the “biosampler”.
6. Section 2.1.2, please provide more details on the reaction mixtures used, such as pH and buffer used, and any other additives/components.
7. Section 2.1.4 is not really a methodology section. It should come after the validation section.
8. Line 238-239, please provide a reference to support this statement. Smaller particles can contribute significantly to PM mass in some environments (e.g. traffic sites) and therefore a discussion on the collection efficiency of the instrument in this case should be added
9. Line 249: resumed -> summarized
10. Table 2, please add particle size and concentration
11. Line 271: Fenton-like reactions are not the only reactions that transition metals can do that contribute to OP. Some metals can oxidise directly for example.
12. Line 272, what do you mean by “heterogenous values” in this sentence?
13. Line 277: how does the tested concentration compare to that you would expect in the ambient?
14. Section 3.2.1, my understanding is that the instrument is designed to capture both soluble gases and PM. In this respect, ozone would not be an interference. Please clarify.
15. Line 299, is the AA depletion comparable to that of the blank measurements or just constant over the O3 concentration range tested? Is AA stable over 2-weeks of unattended operation? In my experience, AA solutions are not stable for more than a couple of days.
16. Why ozone interference is not discussed for the DTT assay?
17. Line 313, how long for was the extraction?
18. Line 320, r2 values look decent but by looking at the plot I would say that the linearity is at an acceptable level for the intended purpose rather than state that the response is linear. Fig 5b does not look linear by eye. And others, like Figure 5a, 5d and 5f also look like they have some deviations from linearity. I suggest running a statistical test.
19. Figure 5e and 5f, why were the filters from the two environments tested only one one assay each rather than both? It would have been nice to see both.
20. Line 342, the non-zero intercept looks to me that it could be due by a deviation from linearity.
21. Line 357, why using amounts in mol rather than concentrations?
22. Figure 6, I can see a deviation from linearity at low and high concentrations in a and b. Part c does not look linear to me.
23. Figure 7, why not test both filters with both assays? Why do you have such a large horizontal error bar in panel a?
24. LODs are missing from the validation.
25. It would have been nice to see an apportionment of the contribution of soluble gases vs. PM to the OP. Why was that not considered?
26. The ozone concentrations measured during the field campaign were higher than the level tested in the lab as it can be seen from Figure S9. Could there be an interference there? It would be nice to expand the tested range in the lab.
27. Line 461, I would argue that linearity was not always “good”.
28. There are several duplicate references, such as Dominutti et al 2024/2025, Dovrou et al 2021a/b, Fang et al 2016a/b, Fang et al 2015a/b, Pietrogrande et al 2022a/b, Rao et al 2020a/b, Yu et al 2020a/b