General comments:

The authors collected ambient PM filters from Davis and diluted the extracts to measure the production of photooxidants (OH, 3C* and 1O2*) as a function of dilution. Essentially, the authors are extending Figure 5 from their previous contribution on this topic: (Kaur et al., 2019). Despite the apparent simplicity of this task, the experiments are tedious and difficult and require a carefully controlled understanding of the probes used and their reactivities (which was published recently in what could be called a companion paper in (Ma et al., 2023)). The results of this paper are important as our community tries to understand the relevance of 1O2* and 3C* photooxidants. I commend the authors for the diligent experiments presented. Yet, there are important revisions required before publication. They are related to additional references, listing of additional controls and restructuring the discussion between the 2 filter types collected.

Important issues to address:

The authors have a winter filter composite (WIN) taken from Feb 5-28 2020 and a summer filter composite taken from August 21-24 2020, which are part of the dilution series. They then make seasonal comparisons between these two filters. However, there is little basis on a seasonality discussion with so few filters over such a short period of time. Instead, I would recommend that the authors focus their discussion on brown carbon and how brown carbon from wildfires (SUM) produce different photo-oxidants than brown carbon from wintertime burning (WIN). Concretely, the revision I’m suggesting involves removing the discussion between lines 267-288, and instead expanding further the discussion included between lines 288-293, as well as changing the discussion throughout the text/abstract/title to focus on a BrC-type intercomparison (which also nicely compares to the wintertime PM extracts in (Bogler et al., 2022)). This story re-design would enable a deeper discussion on the possible nature of the 3C* compounds, which I think would be more beneficial to the community and the future reader.

An important reference is missing which includes recommendations on R_abs calculations and how to use wavelengths from 300 to 800 (instead of to 450 like the authors did in table S1): (Ossola et al., 2021) and their Table 4.

Important references on photoproduced oxidants in PM and rainwater are missing from the paper and really should be included and discussed (and even added as data points to comparison graphs). I don’t see any reason to omit these references:

(Leresche et al., 2021)

(Li et al., 2022a)

(Li et al., 2022b) – this reference is also important for the context of trace metals hypothesized by the authors on lines 320-321. And I would also add (Cote et al., 2018) for a discussion on the role of road dust which is rich in transition metals.

Rainwater photooxidants: (Albinet et al., 2010; Hong et al., 2018)

1O2* reactivity in aqueous extracts (not be plotted on a graph, but worthwhile for the 1O2 reactivity discussion in section 3.3.3.: (Barrios et al., 2021)

Recent review on ALW: (Carlton et al., 2020)

I commend the authors on a thorough study of these oxidants which are difficult to measure. The authors have performed a number of important controls. However, I have additional questions related to the experimental procedure that would need to be clarified before publication:

• What was the source of the H2SO4? Purchased H2SO4 is often brown in color and so addition of the acid (although valid to similar more acidic aerosols) could also be adding chromophores. Could the authors share their controls related to the addition of the acid?
• How were the filters collected and stored in reference to (Paulson et al., 2019) who observed a burst of OH production upon illumination? (The authors do reference this paper in relation to photo-Fenton chemistry on lines 351-352.)
• Did the authors distill their FFA? (Ossola et al., 2021) describes on page 4114 that FFA oxidizes to form a yellow product which can absorb light and lead to inaccurate 1O2* interpretations. If the authors didn’t, then they could run an experiment with and within distilled FFA and propagate that difference through to the measurements they’ve already made.
• Were filter blanks subtracted from the result tables in the SI?
• The inhibition experiments are very good and well described in the SI. What do the authors think is causing the inhibition? Anti-oxidants in DOM? A short discussion in the next would be valuable.

I didn’t quite follow the discussion on “plateauing” of 3C* for 1O2* curve shapes on lines 426-431 and in lines 433-438. Where did the 5000 mgC/L come from? Have the authors considered calculating the % contribution of DOC as a sink for 1O2 in their FFA experiments? If the steady-state concentration is known, the FFA reactivity is known and the water deactivation constant is known, than the authors could potentially quantify the contribution of the DOC as a sink as a percentage. This information could also be discussed along with Figure 6a (a key figure in my opinion!)

In figure 2, why do the 3C* in the WIN and SUM measured by syringol collapse onto one another but that’s not the case of PTA? I suspect there is an interesting BrC-type specific discussion to be addressed here and how perhaps as a community we ought to be using multiple 3C* probes for our measurements?

I also have some criticism on the length and tone of the manuscript. I spent more time than I had allocated going through this manuscript, and I referred often to the SI, as well as had to reference constantly to (Ma et al., 2023) as well as to (Kaur et al., 2019). It’s a difficult read for someone unfamiliar with these types of measurements (like 1^st year graduate students for example). To improve the more editorial side of this manuscript, the authors could consider:

1. moving more information to the SI and focus on the interpretation of their results.
2. Include more references to measurements in their Figure 2. (Manfrin et al., 2019; Bogler et al., 2022) has measurements of OH and 1O2. (Leresche et al., 2021) et al also has measurements of OH and 1O2.
3. Use the full name of the molecules. I often got confused with DMB, PTA and TMP and had to refer back to the methods a couple of times. (There are no space limits in ACP, so perhaps worth considering writing the compound names in full? “trimethylphenol”)

Specific/technical comments:

• The title could include the term “brown carbon” to highlight the differences between filters more accurately.
• Lines 93-94 refers to the authors’ previous work. Why didn’t they do these corrections in the past? If the answer if they learned as they went, then they might benefit from “building” upon their work instead of “criticizing” their work.
• Lines 108 and 109 seem to contradict themselves about which type of PM was collected. PM2.5 or PM10?
• Contrast the statement on lines 419-421 about how DOC is a good predictor of 1O2 (where others have also shown the same like (Cote et al., 2018)) and lines 266-267 on how the water extraction only removes a fraction of BrC.

References:

Albinet, A., Minero, C., and Vione, D.: Photochemical generation of reactive species upon irradiation of rainwater: Negligible photoactivity of dissolved organic matter, Sci. Total Environ., 408, 3367–3373, https://doi.org/10.1016/j.scitotenv.2010.04.011, 2010.

Barrios, B., Mohrhardt, B., Doskey, P. V., and Minakata, D.: Mechanistic Insight into the Reactivities of Aqueous-Phase Singlet Oxygen with Organic Compounds, Environ. Sci. Technol., 55, 8054–8067, https://doi.org/10.1021/acs.est.1c01712, 2021.

Bogler, S., Daellenbach, K. R., Bell, D. M., Prévôt, A. S. H., El Haddad, I., and Borduas-Dedekind, N.: Singlet Oxygen Seasonality in Aqueous PM10 is Driven by Biomass Burning and Anthropogenic Secondary Organic Aerosol, Environ. Sci. Technol., 56, 15389–15397, https://doi.org/10.1021/acs.est.2c04554, 2022.

Carlton, A. G., Christiansen, A. E., Flesch, M. M., Hennigan, C. J., and Sareen, N.: Multiphase Atmospheric Chemistry in Liquid Water: Impacts and Controllability of Organic Aerosol, Acc. Chem. Res., 53, 1715–1723, https://doi.org/10.1021/acs.accounts.0c00301, 2020.

Cote, C. D., Schneider, S. R., Lyu, M., Gao, S., Gan, L., Holod, A. J., Chou, T. H. H., and Styler, S. A.: Photochemical Production of Singlet Oxygen by Urban Road Dust, Environ. Sci. Technol. Lett., 5, 92–97, https://doi.org/10.1021/acs.estlett.7b00533, 2018.

Hong, J., Liu, J., Wang, L., Kong, S., Tong, C., Qin, J., Chen, L., Sui, Y., and Li, B.: Characterization of reactive photoinduced species in rainwater, Environ. Sci. Pollut. Res., 25, 36368–36380, https://doi.org/10.1007/s11356-018-3499-4, 2018.

Kaur, R., Labins, J. R., Helbock, S. S., Jiang, W., Bein, K. J., Zhang, Q., and Anastasio, C.: Photooxidants from Brown Carbon and Other Chromophores in Illuminated Particle Extracts, Atmos Chem Phys, 19, 6579, 2019.

Leresche, F., Salazar, J. R., Pfotenhauer, D. J., Hannigan, M. P., Majestic, B. J., and Rosario-Ortiz, F. L.: Photochemical Aging of Atmospheric Particulate Matter in the Aqueous Phase, Environ. Sci. Technol., https://doi.org/10.1021/acs.est.1c00978, 2021.

Li, J., Chen, Q., and Guan, D.: Insights into the triplet photochemistry of atmospheric aerosol and subfractions isolated with different polarity, Atmos. Environ., 290, 119375, https://doi.org/10.1016/j.atmosenv.2022.119375, 2022a.

Li, J., Chen, Q., Sha, T., and Liu, Y.: Significant Promotion of Light Absorption Ability and Formation of Triplet Organics and Reactive Oxygen Species in Atmospheric HULIS by Fe(III) Ions, Environ. Sci. Technol., 56, 16652–16664, https://doi.org/10.1021/acs.est.2c05137, 2022b.

Ma, L., Worland, R., Tran, T., and Anastasio, C.: Evaluation of Probes to Measure Oxidizing Organic Triplet Excited States in Aerosol Liquid Water, Environ. Sci. Technol., https://doi.org/10.1021/acs.est.2c09672, 2023.

Manfrin, A., Nizkorodov, S. A., Malecha, K. T., Getzinger, G. J., McNeill, K., and Borduas-Dedekind, N.: Reactive Oxygen Species Production from Secondary Organic Aerosols: The Importance of Singlet Oxygen, Environ. Sci. Technol., 53, 8553–8562, https://doi.org/10.1021/acs.est.9b01609, 2019.

Ossola, R., Jönsson, O. M., Moor, K., and McNeill, K.: Singlet Oxygen Quantum Yields in Environmental Waters, Chem. Rev., 121, 4100–4146, https://doi.org/10.1021/acs.chemrev.0c00781, 2021.

Paulson, S. E., Gallimore, P. J., Kuang, X. M., Chen, J. R., Kalberer, M., and Gonzalez, D. H.: A light-driven burst of hydroxyl radicals dominates oxidation chemistry in newly activated cloud droplets, Sci. Adv., 5, eaav7689, https://doi.org/10.1126/sciadv.aav7689, 2019.

The paper aims at predicting photooxidant (1O2, 3C* and OH) concentrations in brown carbon aerosol liquid water. This is an important issue and relatively challenging to extrapolate from dilute laboratory experiments to the more concentrated aerosol liquid water. Here is a few issues and thoughts on the manuscript:

Steady-state concentration of 3C* and 1O2

The review by McNeill and Canonica cited in the manuscript indicates that the steady-state concentration of 3C* and 1O2 are roughly equals one to each other. The authors present numbers that are quite higher for 1O2 than 3C*. I think that the authors should make it clearer that the numbers they measure for 3C* are only a subset of the triplets (oxidizing triplets). This has implications when the authors compare the steady-state 3C* to literature one. The literature concentrations were not necessarily measured with the same probes and are not necessarily the same subset of oxidizing triplets and I do think that one should be careful when comparing 3C* numbers.

Extraction efficiency

To investigate [DOC] influence, the authors extracted the collected PM2.5 in various amounts of water. The authors present convincing evidence that [DOC] reflects the amount of water used in the extraction. Seeing Table S2 and S3, I was left wondering if it is also the case for the inorganics. E.g., Na+ concentration does not look to reflect well the amount of water used in the extraction. Similarly, the measured OH sinks do not look to reflect well the dilution. Seeing Figure 2, I think that for 1O2 and 3C*, the results do not look to be affected by a potential variation in extraction efficiency. But for the OH measurements, I am wondering if the observed increase is real or if it reflects a variation in the inorganics extraction (or eventually a non-ideal behavior of the probe, see below).

OH Probe

Benzoic acid is known to have some drawbacks as OH probe. Being relatively less selective towards OH than other OH probes (Environ Chem Lett (2010) 8:95–100). The observed increase in OH concentration could also reflect a non-ideal behavior of the probe (e.g., if the probe starts to react with 3C* at high [DOC]). If the authors have the possibility to do additional control experiments, I would suggest replicating an OH measurement at high [DOC] in the presence of an OH quencher. That would tell the authors if the observed production of p-hydroxybenzoic acid is due exclusively to OH reaction.

1O2 vs 3C* reactivity

When comparing 1O2 vs 3C*, the surface water literature indicates that 3C* tends to be more important for the degradation of contaminants (Environ. Sci. Technol. 2013, 47, 10781−10790, Environ. Sci. Technol. 2013, 47, 6735−6745). I am not very sure for which class of compounds 1O2 reactivity tends to be higher than 3C* but the examination of the compounds presented in Environ. Sci. Technol. 2013, 47, 6735−6745 indicates to me that it may not be electron rich compounds as the authors stated on line 85. Electron rich compounds have very high 3C* reactivity that would dominate 1O2 pathway. It may be compounds that are doing Diels-Alder reaction with 1O2 that reacts preferentially with 1O2.

Halogens influence

A side thought to consider for further works:

The authors (Anastasio, C., and J. T. Newberg (2007), Sources and sinks of hydroxyl radical in sea-salt particles, J. Geophys. Res., 112,) and others (Environ. Sci. Technol. 2021, 55, 13152−13163) measured sinks of OH such as Cl- and Br-. It would have been interesting to evaluate Cl- and Br- importance as OH sink. Additionally, Cl- and Br- can quench 3C* (PNAS, 2016, 113, 21, 5868–5873). These reactions would form bromine and chlorine radicals that have some reactivity and could potentially lead to the formation of brominated and chlorinated products. This has some similarities with the formation of disinfection by-products during water treatment and the produced compounds could potentially have a high carcinogenicity.

In this new contribution, Ma et al explore different sources of tropospheric aqueous oxidants, including hydroxyl radical (●OH), singlet molecular oxygen (1O2*), and oxidizing triplet excited states of organic matter (3C*), as a function of the aerosol liquid water (ALW) for two distinct samples (i.e., winter vs summer) sampled in California. Obviously, the amounts of oxidants in the tropospheric liquid phase is poorly constrained, and therefore this contribution provides valuable information, that will certainly be subject to discussion. But this is sign of the usefulness of the data provided.

This manuscript is well written and illustrated, and reads very well. This reviewer enjoyed reading it, and would recommend its publication subject to minor corrections.

Due to the very limited water content of particles, it is difficult to quantify oxidant concentrations in ALW directly. To predict these values, the authors measured photooxidant concentrations in illuminated aqueous particle extracts as a function of dilution and used the resulting oxidant kinetics to extrapolate to ALW conditions. How were such dilution ratios defined? Do they have any atmospheric significance?

Data are reported in the range 0-500 mg C/L. At the higher concentrations, what precautions have been taken to maintain a constant oxygen concentration or is oxygen consumed during the illumination experiments? With regard to the important role played by oxygen, I would suggest to clarify this.

The extraction procedure used is very simple and certainly samples a subset of the brown carbon available. How is this affecting the conclusions of this study? Are the numbers provided to be considered as lower limits only? In fact, would using other extraction conditions (different pH, etc.) enhance the amount of absorbing and reactive material?

It is show that the summer extracts absorb sunlight at approximately twice the rate as winter extracts. Is this expected? Was this sampling affected by strong biomass burning occurring in California over the last years? If yes, this should made clear as the seasonality of the two samples considered would be affected and the overall outcomes of this study as well (it would not correspond to a summer vs winter comparison, but rather to two types of burning processes).

This reviewer had difficult to follow the logic between equations 1 to 6, and would recommend providing more explanations on the arithmetic used here.