The manuscript aims at measuring the seasonal variation in photooxidant formation and concentration in atmospheric water and to predict the lifetime of 5 compounds in the atmosphere. Overall, I found the article well written and would support its publication as it brings interesting information to the community.

I did not find major issues in the article, here is my list of comments and corrections:

Abstract and introduction

The abstract and introduction are clear. In addition to singlet oxygen, excited triplet states and hydroxyl radical, the authors could also mention in the introduction other photooxidants that were not considered in the study but that may play a role in the transformation of some classes of contaminants. E.g., Halides radicals may play a role in the transformation of electron rich compounds (Marine Chemistry 115 (2009) 134–144) or long-lived photooxidant could be important for the transformation of phenols or anilines (Water Research 213 (2022) 118095).

L25. It looks to me that the OH quantum yield value is too high and does not correspond to the values presented in the article (Table S3).

L.79. I would switch organic compounds for DOM as the quoted studies presents correlations between 3DOM* quantum yields and factors correlating with the molecular weight / aromaticity.

Material and methods

L.141. I would indicate the spectrophotometer cuvette pathlength.

l.146 I would add in the SI the arc lamp spectra, that is important to evaluate nitrate photolysis.

Results and discussion

The results are presented in a logical order, I have two main comments on the results:

1. Hydroxyl radical quantum yields are presented. The fact that hydroxyl radicals are produced by many pathways in the atmospheric aqueous phase, and that each pathway has its own quantum yield, makes the numbers difficult to compare to other studies and not that useful. The quantum yield numbers would depend on the extract’s composition (nitrate, nitrite, iron) but also on the irradiation wavelength distribution.
2. Part 3.5. It looks like the authors use Henry constants to evaluate the partition of 5 compounds between the atmospheric aqueous phase and the gas phase. The use of Henry constants is fine for dilute solutions, but I fear that for concentrated solution (1ug PM/ug H2O), the actual partition may be different from the one calculated using Henry constants. I think that the authors should at least acknowledge the problem. If the authors are aware of methods or measurements to evaluate the actual partition coefficients to use them instead of Henry constants.

Figures, the date format may confuse non-American reader (e.g., one can read the first date as November first 2019 or January 11^th 2019). I would suggest writing the months to be clearer. Also, the numbers on the y-axis could be written as 1×10^-15 (and not 1E-15).

L.306. “fresh BB are fragmented during aging”, it could be noted that ozone exposure also induces and increase of E2/E3 (Leresche et al. quoted in the manuscript) and that ozone indeed also induce a decrease in mean molecular weight indicating that fragmentation occurs during ozonation (Environmental Science & Technology, 2023 57 (14), 5603-5610).

L.347. DDT assay, the abbreviation is not defined, switch for the full name.

L.450. Do the authors think that there are anilines moieties in PME ? I would suggest withdrawing the mention to anilines.

L.508. The second-order rate constant between singlet oxygen and water was reevaluated to be of 2.76*10⁵ M^-1 s^-1 (Environ. Sci.: Processes Impacts, 2017, 19, 507–516) I would suggest using the more recent value.

L.552. ³C* fraction that produces singlet oxygen (fΔ). This fraction was recently measured for Suwannee River fulvic acid to be of 0.34 (Environ. Sci. Technol. 2017, 51, 13151−13160). The value from McNeill and Canonica is a rule of thumb I believe. It would be worth mentioning this 0.34 value.

L.678. “Estimated concentrations of ¹O₂, ³C*, and OH in ALW are on the order of 10-12 - 10-11, 10-13 - 10-12 and 10-14 M”. I would suggest putting the respective number range next to the corresponding reactive species, as it is, it is difficult to see which numbers correspond to what.

L.993 and L.66, it should be Hoigné and not Hoigne.

Overview:

The authors of this manuscript present OH, 3C* and 1O2* measurements of 18 filters taken from Nov 2019 to Oct 2020 in Davis already described and published in (Jiang et al., 2023). In Jiang et al., the concentrations of OH, 3C* and 1O2* are presented for each filter in Figures 5, 6, S11, S12.

The authors of this manuscript present MAC values for their extracts, the same values as in (Jiang et al., 2023). They also discuss the AMS data from (Jiang et al., 2023). The quantum yields are also discussed in (Jiang et al., 2023). Finally, the authors extrapolate the OH, 3C* and 1O2*  concentrations to aerosol liquid water content, which they already did for 2 of the same samples in (Ma et al., 2023b).

Therefore, this paper is not publishable as all the data has been previously published across two papers by the same authors: (Ma et al., 2023b; Jiang et al., 2023).

Comments:

Nevertheless, the techniques used, although uncommon in the community (like use of D2O for FFA, use of double probe for 3C* -  although that’s building on their own previous work in (Ma et al., 2023a) which has interesting merit -, acidifying to pH4.2 with no clear understanding of the impact of pH), have been reported in other publications by the same authors. The data are listed in tables in the SI in a good and extensive matter (but missing LOD info). Unfortunately, there is no new key message or finding in this submitted manuscript in comparison to previously published work by the same group, and the paper has important issues that would need to be resolved.

General issues with this paper beyond the lack of new data/results are listed here:

• Raw data of all the BA, FFA, SYR and PTA probe decays for all the samples is missing.
  • There is one example of the BA decay which for the 121719 and the 030420 samples is clearly not linear. This observation is concerning as the deviation from linearity indicates that the oxidant is no longer under pseudo-first order rate kinetics! What do the probe kinetics look like for other oxidants and other filters?
• A number of incorrect statements are used to motivate the study, often based on “things being unknown”. Here are examples:
  • Lines 68-69: So much is known about measured and modeled OH radical concentrations in the gas phase and its seasonality (Martin et al., 2003; Fan and Li, 2022) and so simply by partitioning, one could estimate what the seasonality might be (I would agree with a statement about OH radical concentrations being variable due to different sinks, but the word “unknown” is a disservice to the OH radical community (ex: Comprehensive OH seasonality by (Pfannerstill et al., 2021) and OH has been quantified at the global scale: (Thames et al., 2020) and (Pimlott et al., 2022) are examples.
• References are an issue throughout the text where multiple papers (5-6) are referenced without identify the contribution of each and thereby missing the opportunity to build upon previous work. Here are a few examples to support this claim:
  • Lines 53-55: 6 seemingly random references are listed to support the fact that OH, 3C* and 1O2* are important oxidants. Reviews such as (McNeill and Canonica, 2016; Ossola et al., 2021; Hems et al., 2021) are more appropriate
  • Statement on Lines 98-99 is inaccurate as (Bogler et al., 2022) addresses both the seasonality and the particle type.
  • Line 263: a study from 2001 and from 2013 were chosen to discuss organic carbon content in biomass burning, when there are more recent references: to name a few: (Fang et al., 2023; Di Lorenzo et al., 2017; Lee et al., 2016; Bikkina and Sarin, 2019; Forrister et al., 2015)
  • Same point is true for line 281-283 where the 4 references listed are not representative of the statement, see for example (Fleming et al., 2020; Lee et al., 2014; Laskin et al., 2014)
  • Another example on lines 284-285
• The authors chose to focus on a seasonality story line, but was 2020 representative? There were massive wildfires in Fall 2020 in northern California.
  • Where did the PM2.5 data in Figure 1 come from? (I found it at the bottom of Table S1 in footnote b…but it should be in the text and appropriately referenced with multiyear data)
  • What is the seasonal PM2.5 profile in northern California? Was 2020 representative of PM mass?
  • The methods sampled PM10 – how different/similar are PM10 to PM2.5 in Davis.
• There were no samples taken between March 4^th 2020 and July 7^th 2020 (Table S1) and there are therefore no spring samples. The use of spring seasonality is therefore unjustified throughout the text.
• The authors motivate their work discussing Fenton OH chemistry (lines 61-64) but how do they take this chemistry into account in their own measurements of OH steady state concentration calculations?
• Relevant work that should have been built upon to connect to ROS and EPFRs (also from ambient Californian samples): (Fang et al., 2023)
• No mention of limits of detection. What are the minimum concentrations that the authors are able to quantify (3 sigma above background)?
• The authors decided to divide their concentrations by 7 for comparing filters collected for 7 days and filters collected for 1 day. This division is an oversimplification of the complex mixture of brown carbon and is not justified.
• Line 15: The abstract mentions that; “there are few measurements of these photoxidants…” which is not accurate. There are likely over a dozen: (Faust and Allen, 1992; Anastasio and McGregor, 2001; Albinet et al., 2010; Hong et al., 2018; Cote et al., 2018; Manfrin et al., 2019; Kaur et al., 2019; Leresche et al., 2021; Jiang et al., 2023; Bogler et al., 2022; Lyu et al., 2023; Ma et al., 2023b)!
• The mathematical equations representing the projected concentrations in AWL are missing.
• Presentation of wildfire information in lines 231-236 but making no connection to the oxidant data.
  • Wouldn’t a discussion on the different BBOA samples have been more worthwhile for the community?
• There is considerable research undertaken to study the impact of solvent extraction on filters that the authors should be building upon: (Chen et al., 2022) and references therein. (referring to line 314)

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