Yu et al report on extensive measurements of PM2.5 OP (oxidative potential) based on an analysis involving 5 different acellular approaches. The analysis was performed on samples collected at a number of sites in the midwestern US and the paper reports on comparisons between the assays and PM2.5 mass.  It is stated that a second paper will focus on the PM2.5 chemical components driving these results.  The paper is based on a substantial amount of work and provides more insights into the utility of current ways to characterize OP, and it also sheds light on the potential usefulness of using these assays in health studies.

A major conclusion is that the poor correlation between all the various assays, when compared at one site, (and this is largely true for all the sites), implies all these types of OP assays are needed for health studies.  One could also conclude, that all of these assays (except possibly one) are each deficient, and no ideal assay exists.  It may also even suggest that if no comprehensive OP assay is available, then maybe the approach is flawed since the goal of using these assays was to develop a comprehensive single measure of aerosol toxicity. Since this group of assays appears to fail in demonstrating this goal, instead maybe one should focus on the specific species that drive OP and not use these assays?  How does one know if even more assays are needed to fully characterize PM2.5 OP? Furthermore, how would all these various OP measurements, even if available to health researchers, be utilized in a health study, ie how would they be combined to give an overall better indicator of PM2.5 OP?  These questions are important and should likely be considered; a discussion beyond the conclusion that all these assays should be utilized, is warranted

The data do support other studies showing variability between various OP measures and PM2.5 mass, suggesting PM2.5 mass is a poor predictor of the ability of particles to cause oxidative stress (assuming these assays are good measures of OP).  This is an important finding.

Comparisons between sites using different samplers operating at the same time depends on some level of measurement precision to argue that observed differences (poor correlations) are really due to differences in aerosol particles at the sites.  This applies to the gravimetric measurement of PM2.5 mass and the various OP measurements.  The authors do discuss variability in the negative and positive controls, but the data shown in Table 1 is only the precision of the analysis and does not consider sampling, filter storage or extraction.  Can it be stated that this precession for all the species measured and PM2.5 mass is significantly better (lower variability) than that of the comparisons between sites.  It would be especially interesting to know the precession of the methanol extracts, which based on the extraction approach is likely the most imprecise measurement (curiously it also shows the least variability between assay results from various sites). A more comprehensive discussion is warranted that includes specifically addressing if the differences seen are real or just noise.

One conclusion that may be drawn from this work and which is consistent with past studies is that the DTT assay is the most comprehensive measurement of OP (see, for example, discussion in lines 289-407). This may be because DTT includes electron transfer reactions from both organic species and metals, whereas AA, GSH and production of OH in the various assays is likely largely driven by metals.  One could actually discuss an interpretation of the data in which the most assay meets the goal of being the most comprehensive. For example, maybe instead of arguing that all assays in their various forms are needed, one could try to assess which is best?

Specific Comments.

Line 20-21, not sure how higher site to site correlations proves methanol extracts includes more insoluble species?  The idea that methanol extracts a greater fraction of OP than water is well known.

Lines 142 to 148, Charrier et al (2016) suggest a mass concentration for measurement of OP to limit nonlinear effects of 10ug PM/mL, here the authors use 100 ug/mL, why and what is the effect of doing this, ie does it solve the nonlinear problem?

It would be useful to provide the composition of the simulated lung fluid.

One issue with current measurements of OP by the various methods is that there is a range of approaches used for each of the methods.  This makes comparisons between this work and other studies complicated. It would be valuable to know exactly how these various methods compare to what has been utilized in other studies.  For example, maybe a table in the supplement could provide more details on the methods used here links to past studies that used the exact same approach.

Line 238-239, this statement should be supported with data.

Line 274, typo, change “into” to “in”?

How do the authors explain the data where OP in water extracts is greater than OP methanol when it is established that methanol extracts water soluble species plus organic species?  Seems this result demonstrates the lack of precision of the methanol method. Or are the authors implying that some water soluble species that contribute to OP are not extracted and detected in the methanol method?

What is the difference between methanol soluble OP and methods that attempt to measure all OP, eg, that associated with surfaces of solid particles?

In this work, the authors measured oxidative potential (OP) of particulate matter in five urban areas in midwestern US. Particulate matter (PM) is a significant health hazard, and its oxidative potential is thought to be representative of its toxicity. The authors assessed oxidative potential in 5 different endpoints on a weekly basis. These OP measurements are often difficult to make, but the authors had developed a system to automate the measurements of PM on filters. The results from the study showed large variabilities across sites and endpoints, and these variabilities, along with poor correlation with PM mass, suggest that PM2.5 mass alone is a poor indicator of potential health impacts. The discussion of the results was not very deep, and, in many cases, more detailed exploration is encouraged to better understand these results. In general, the manuscript is well written, but some of the main messages can be more clearly communicated, rather than buried in a lot of numbers and text. I believe that this manuscript should be published in ACP after some major revisions.

Major comments:

In general, this work reads like a measurement report. I was very impressed by the ability to make all these measurements, but somewhat disappointed with the lack of insights from the measurements. More specifically:

-    A lot of information about each site was given in Section 2.1, but when discussing the spatiotemporal variability, there is virtually no discussion in these contexts in Section 3.3. Why does CMP behave so differently? What are the spikes? The same goes for Section 3.5, where the site-to-site comparison is discussed in the context of some statistical measures (correlation coefficient, COD). Again, what are the physical insights? 

-    Lines 257 to 280 were very hard to follow. The discussion jumped around from OP measure to another (sometimes mass-normalized, other times volume-normalized). The OP endpoints from this particular study were compared to those reported in the literature, but the discussion focuses on very shallow comparisons (e.g. higher, lower, different, the same). I am very confused about the purpose of this discussion: are these comparisons meant to validate the measurements? Are they meant to highlight the differences to illustrate differences between sources, or site characteristics? Are we expecting the OPs to be the same, or different from previous studies? My suggestion is to focus on some main message, and then show the comparisons that illustrate the point.

-    How are we supposed to make sense of the large differences between the various endpoints? They are different measures and operate differently, so they are expected to be different. So, if they are significantly different, then what? The suggestion from the authors is to measure all of them, but then how do we make sense of the different numbers, or trends? A closer examination of what each OP is measuring (and what chemical components are most linked with each measure) would be useful.

-    Given that ACP is an chemistry-focused journal, I believe that discussion of chemical composition is well within the scope of this manuscript, and should not be separated for a later publication. Chemical composition is central to many of the questions I posed, and including some information of composition is necessary to make sense of these measurements. 

Minor comments:

-    Line 18 and elsewhere: it might useful to define what volume means. Presumably this is air volume, not particle volume

-    The introduction is very well-written and reflects the current state of knowledge.

-    Lines 85-93: this might be a good place to define some research questions and hypotheses, and address them accordingly at the end. It will help with adding some depth to the discussion and going beyond just reporting measurements.

-    Line 100: “Chicago, Indianapolis and St. Louis” seem redundant.

-    Section 2.2: are the methanol extracts also kept the same PM mass for OP measurement? In the water soluble extract, the volume of water was adjusted to achieve the same mass; how was this done for the methanol soluble extract?

-    Line 160: when the dried methanol extract was reconstituted in water (DI water), are there insoluble components? For example, I can imagine some organic compounds are extracted by methanol and stick to the walls of the vial when dried, but does not dissolve in water during reconstitution. 

-    Lines 235-236: 5.7-21.7 does not seem to be significantly higher than 2.0-20.2. Perhaps show the median?

-    Lines 240 and 281: how is the “time series” different from the temporal variation in “spatiotemporal variation”? There are a lot of overlapping points between Sections 3.2 and 3.3, and these sections are be significantly combined and condensed for easier reading. Or perhaps the author intended the discussions to be separate, and if so, it would be good to convey the differences in the section titles.

-    Line 248-249: Just want to confirm: In line 217, the July 4th data were excluded from the regression analysis, but are included here in the discussion. It is a little confusing; perhaps some slight clarification would be useful.

-    Line 294: why is different from SE US? The seasonal trend seems to be related to photochemical activity (higher in the summer). In general, the midwestern US provides an interesting contrast to previous studies because it has larger temperature differences between summer and winter.

-    Line 350-355: this seems like a somewhat handwavy explanation for an anomaly, not really supported by evidence. What is the evidence for significant alkaloid compounds at this one particular site? Are there other studies that show Cu can complex with organic compounds and reduce OP?

-    Lines 356-368: why focus on Fe-organic complex? The simpler explanation would be organic compounds that contribute to OP that extracted in methanol but not in water.

-    Section 3.6: My suggestion is to point out that current regulations focus on PM mass only, and these results show how inadequate this approach may be. (The reason I suggest this is, at first, I felt it was obvious that OPm would not correlate with PM mass and was somewhat puzzled by the need to do this analysis. But upon second thought, this analysis is useful in a regulatory context.)

-    Line 474: “the results … provide”, not “provides”

-    Figures and tables are generally too complex