Zhou et al. describe a series of laboratory flow-tube experiments analyzing sulfate formation via heterogeneous reaction of SO2 and several types of photo-active organic particles. The results are interesting, demonstrate the utility of a novel analytical method (single-particle aerosol mass spectrometry) for observing particle-phase sulfate formation, and add to the rapidly growing body of works exploring atmospheric sulfate formation. I believe this paper merits publication in ACP after several major and minor comments are addressed, potentially involving additional experimentation. My comments are outlined below.

Major comments

I believe the authors need to more clearly highlight the apparent role of RH in these experiments and to more thoroughly explore the role that RH plays in the observed reactions. At line 221 the authors discuss that vanillin-coated particles produced substantially less sulfate at 20% RH relative to the 80% RH used in other experiments. RH therefore seems to be an important factor in affecting organic photosensitizer-initiated sulfate formation, but RH isn’t mentioned as a factor in the abstract or the experimental description in the introduction. More thoroughly investigating the role that variable RH has on photosensitizer-initiated SO2 oxidation would be very important to better understanding the significance of this pathway in ambient environments. Additionally, at line 158 the authors discuss potential SO2 oxidants and note the possibility for oxidants that form from H2O; does the apparent RH dependence point to H2O as a secondary oxidant source following initial photo-excitation?

I have several questions about sulfate signal variability, mass spectral variability inherent to the SPAMS, and particle size.

• Line 110, section 2.2: how much variability are there in SPAMS spectra? E.g., how much variability in absolute peak area would be expected for monodisperse sulfate particles? What is the expected detection efficiency of the SPAMS for the observed size ranges of particles? Is it possible that any of the presented results are biased from low number statistics due to low particle detection efficiency and/or low numbers of particles? Does particle-phase water have any effect on desorption/ionization and RPAs/APAs? Even if some of these aspects of the SPAMS have been discussed in more detail previously some discussion here is necessary to fully understand and evaluate the presented results.
• There seems to be a lot of spread in the sulfate RPAs within the experiments (Line 146/Figure 2). Do the authors have a theory for this spread? Is SO2 oxidation less efficient on some particles? Is there substantial spread in flow tube residence time? Is this just due to particle-to-particle variation in SPAMS ionization?
• On lines 172-174 the authors discuss an apparent size component to the efficiency of sulfate formation. Figure S4 clearly shows that the SPAMS sizing effectively captures the expected size distribution of the PSLs, but what size range do organic-coated particles span before sulfate formation begins? To put another way, how uniform is the population size distribution after becoming coated in organics? Do these results suggest that sulfate formation occurred unevenly across the particle population? Are there any instrumental factors that may influence the apparent size-dependent sulfate production efficiency? E.g., is it possible that larger particles are only partially ionized by the SPAMS and this skews the observed RPAs?
• At lines 209-211 the authors discuss the difficulties in using absolute peak areas to draw conclusions about sulfate signal. Are there circumstances where it would be feasible to translate the absolute peak area to some mass (or mass range) of sulfate and therefore be more quantitative about the amount of sulfate present in a particle? Would this be possible after observing APAs of size-selected sulfate particles and taking into account particle sizes measured by the SPAMS? Alternatively, is there a way to be reasonably quantitative about sulfate production rate from the studied photosensitizers, based on measurements like the amount of depleted SO2 and particle surface area?

The authors note on lines 174-176 that the sulfate formation efficiency follows a similar trend as SOA formation from reaction between the three photosensitizers and syringol. What did the authors of the previous works attribute the difference in SOA production to? Would this be reasonable within the current system? Are there any other reasonable parameters that would influence the efficacy of SO2 oxidation by these photosensitizers? E.g., absorption spectra, quenching efficiency, particle phase state or physical attributes.

Minor comments

General: I suggest adding subsections to the “Results and Discussion” to more clearly organize the different materials in this section, as some of the transitions within and between paragraphs are abrupt.

Line 58: what properties make vanillin a typical aromatic carbonyl sensitizer? Or is it just a photosensitizer that's often used in studies?

Lines 85-86: is the estimated organic coating thickness shown anywhere?

Line 151: what is the presence of (minor) sulfate under dark conditions attributed to?

Line 155: are any sulfite (SO3) signals observed in the mass spectra? It doesn’t appear so based on Figure 1 but it’s a little difficult to tell. Would sulfite signals be expected to be visible while examining heterogeneous SO2 oxidation?

Line 179: can the O2-free environment influence any aspect of the ionization process?

Line 181: although the absolute changes in RPA are smaller for syringaldehyde particles, is the relative change similar to that for vanillin and DMB? Additionally, do the results in N2 imply that direct 3C* oxidation of SO2 can occur but is slower than pathways with O2?

Line 186: specify what type of system Wang et al. (2020) was exploring.

Lines 188-189: have similar variations in 3C* reactions rates from different sources towards the same analyte been observed previously?

Line 193: can the decrease in organic ion RPA also be consistent with ion scavenging by newly produced sulfate?

Line 195: the location of the material following “Note…” seems odd and incongruous with the rest of the paragraph.

Lines 195-199: the authors seem to be implying that they do not expect the organic-coated PSLs to undergo substantial growth at the RH values used. If this is correct, please state so directly. Any other statements the authors intend to make here on particle physical characteristics should be clearly stated.

Line 203: to clarify, are the vanillin-coated particles here still PSLs?

Line 205: would pH and the identity of the NO3- counterion (e.g., H+, NH4+) potentially influence SO2 oxidation?

Line 210: is there any possibility for the different photosensitizers/organic particle matrices to lead to different sulfate ionization efficiencies and RPAs?

Line 214: it’s not clear that the KNO3 particles are deliquesced. Freney al. (2009) observed continuous growth with increasing RH for KNO3 particles and a deliquescence RH of 90% for dried particles (in line with prior works cited in Freney et al.). Therefore, I don’t believe the direct comparison to the sulfate formation in aqueous droplets used in Gen et al. (2019) is valid, and this comparison and discussion of photosensitizer vs nitrate SO2 oxidation should be caveated with this information.

Line 224: is there a reason to suspect that oxalic acid/KNO3 mixtures might affect SO2 oxidation differently than pure KNO3 particles?

Line 238-239: “qualitatively more efficient” under the studied conditions: wet aerosols at 80% RH.

Line 250: are photosensitizers emitted or formed in non-BB environments, for example urban environments where multifunctional aromatics are common emissions and high NOx levels are common?

Zhou et al. investigated the sulfate formation from aerosol SO₂ oxidation by model biomass burning photosensitizers. The authors show clear evidence that biomass burning-derived photosensitizer particles can induce photosensitized oxidation of SO₂. The results will advance our understanding of sulfate formation pathways and therefore meet the metric for publication in ACP. I have some minor comments for the authors’ consideration.  

Line 25: S(IV) is often used to represent dissolved species of SO₂. Can the authors confirm that the aerosol particles in this study are in the liquid phase?

Lines 85-86: Are the particles uniformly coated? It would be helpful to provide the size distribution information of the coated particles.

Lines 131-137: The authors tend to attribute the sulfate formation to SO₂ oxidation at the aerosol surface. However, the increase of SO₂ consumption with the increase in surface area cannot rule out the possibility of bulk phase reactions. Can the authors provide more insights on whether the reaction occurs at the surface or in the bulk?

Line 138: Can the authors explain why only slight SO₂ consumption was observed in the presence of SyrAld-coated particles? The aerosol pH is also important to SO₂ oxidation. Is the pH of these particles similar?

Lines 202-203: Are the size distribution of particles similar for VL-coated and KNO₃ particles?

Lines 221-223: What is the role of RH? If it is due to the fewer dissolved VL, then it means that the particle is in the liquid phase. Is it in contrast to the discussion in lines 195-199?

Lines 214-217: Are these results applicable to ambient conditions? Does this indicate that nitrate photolysis plays a negligible role in sulfate formation in ambient conditions? 

This manuscript describes studies of aqueous phase oxidation of sulfur dioxide by three photosensitizers, and for comparison, a non-photosensitizing organic compound and the nitrate ion.  The organic compounds are common components of biomass burning plumes, including some phenolic and some non-phenolic species.  The authors show that photosensitizer-mediated oxidation of SO₂ is much faster than by nitrate photolysis.  Pure N2 is also substituted for air in some experiments to provide some clues about the reaction mechanism.  These results suggest that SO2 oxidation by the secondary oxidants (singlet oxygen (¹O2), superoxide (O2 ^.-), hydroperoxyl radical (^.HO2), and ^.OH) produced by reaction of the triplet species with O2 is much more significant than direct reactions between ³C + SO₂.  These results are of interest especially to those studying the puzzle of rapid sulfur oxidation in polluted regions, which is especially notable in humid areas with high aerosol loading.  I recommend publication after minor revision to address the following comments and questions.

The manuscript cites two earlier studies of photosensitizer-induced S(IV) oxidation (Wang et al. 2020 and 2021).  Looking at these earlier studies, it appears that Wang et al. (2020) studied humic acid, ambient aerosol particles, and 4-benzoyl benzoic acid, while Wang et al. (2021) studied naphthalene-derived secondary compounds, so this manuscript advances our knowledge of photosensitizer-induced S(IV) oxidation by testing three photosensitizing aldehyde species, both phenolic and non-phenolic, plus a non-photosensitizing acid species for comparison.  However, readers would benefit from a clearer explanation of how the current study builds on these earlier works in the introduction.  This would also help readers to better understand the statement (page 8 line 188) where the authors try to rationalize the conflicting results about the importance of secondary oxidant species between the current study and that of Wang et al. (2020).

It would be helpful to have the chemical structures of the studied compounds given somewhere in the manuscript or SI along with a listing of which compounds are photosensitizers and which are phenolic.  Currently, the latter bits of information are split between the Introduction and the Methods sections, making it difficult for readers to notice or understand the close structural relationships between the different VOCs selected for study. 

p. 8 line 188: This sentence is the authors’ only attempt at resolving the significant differences in results between Wang et al. 2020 and the current work. Yes, they studied different photosensitizing compounds.  However, given what is known about triplet carbon states and photosensitization, does it make sense that the aldehyde photosensitizers in the current work reacted with SO2 mostly via secondary oxidants, while the carboxylic acid photosensitizers in the earlier study reacted directly with SO2?  Some further discussion here could be very valuable.

p. 9 lines 195 – 199: This argument about solubility, phase, and reactivity is confusing. The authors note that vanillic acid and syringic acid have no measurable hygroscopic growth due to water uptake at 90% RH, and that the three aldehyde photosensitizers are less hygroscopic than these two acids, suggesting that they may therefore be solid or semi-solid phase aerosol particles at the range of RH used in this study.  From the preceding parts of the paragraph, the authors appear to be using this aerosol phase argument as a possible explanation of the lower reactivity of vanillin and syringaldehyde.  However, DMB is clearly less hygroscopic than vanillin or syringaldehyde, and by this argument it should be the least reactive of the three.  In any case, how this aerosol hygroscopicity information ties in to the rest of the paper is not spelled out.

Supplement p 2 line 23:  Was the transmission of the quartz glass vial measured through just one wall, or all the way through the vial (both walls)?  If the latter, the transmission of light to the inside of the vial may be closer to 95%, necessitating a smaller photon flux correction factor.

Technical corrections

p. 7 line 146: this sentence is unclear. What “considerable difference” is being referred to, that between average RPA and NP, between different VOCs, between dark and UV conditions, or between one of those things and the SO2 consumption?  The context of surrounding sentences does not fully resolve the meaning of this sentence.