the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 25 Nov 2025
Multiphase reactions of aromatic organosulfates with OH radicals: Kinetics, mechanisms, and environmental effects
Abstract. Aromatic organosulfates (aromatic OSs) are widely detected in the atmosphere and exhibit high abundance in urban areas. However, the atmospheric fate and environmental impacts of aromatic OSs remain poorly understood. In this study, we investigated the multiphase reaction of three aromatic OS (i.e., phenyl sulfate, p-tolyl sulfate, and 4-ethylphenyl sulfate) with OH radicals. The second-order reaction rate constant (k) of aromatic OSs with OH radicals were measured in the range of 4.29–6.38×109 M–1 s–1 at different pHs. It is found that k values are similar for the homologues of aromatic OSs, whereas are slightly affected by the solution pH values. The multiphase reactions of aromatic OSs and OH radicals mainly yield functionalized OSs, along with fragmented OSs and inorganic sulfate. The observation of inorganic sulfate formation, for the first time, indicates that aromatic OSs can also be converted into inorganic sulfate in analogues to aliphatic OSs. Furthermore, generated chromophores and fluorophores (constituents of brown carbon, BrC) products can significantly enhance the light absorption capacity, particularly under acidic conditions. These findings provide new insights into the understanding of the fate of aromatic OSs in the atmosphere that they can rapidly undergo atmospheric transformation, affecting the atmospheric sulfur cycle and altering aerosol optical properties.
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Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2025-5606', Anonymous Referee #1, 13 Dec 2025
- AC2: 'Reply on RC1', Liubin Huang, 27 Feb 2026
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RC2: 'Comment on egusphere-2025-5606', Anonymous Referee #2, 19 Dec 2025
This manuscript provides evidence that OH oxidation of phenyl sulfate can regenerate inorganic sulfate, and that OH oxidation of aromatic OSs can form BrC products. These are important scientific questions relevant to this journal; however, many claims are made without data to back them despite it being collected. Most notably, products detected with mass spectrometry are only reported for 1 of 5 experiments for which UPLC/LC-MS/MS data was obtained, and ion chromatography data is also only provided for 1 experiment.
I found numerous (>20) grammatical and syntactical errors, and thus I recommend that the authors review the language with a more critical eye and double check their revisions with a grammar checking software. Awkward transition word choices obscured the meaning of many sentences, particularly in the introduction and results & discussion.
Overall, I have many significant concerns about the quality control and experimental methods that need to be addressed before I can recommend this manuscript for publication.
Specific comments
Line 24: It is inaccurate to state that organosulfates constitute “~30% of particulate organic mass,” please rephrase as “up to 30%” or cite specific regions where this mass concentration was measured.
Line 31: “except for isoprene and monoterpenes derived OSs” – confusing wording; were these OSs also detected? Please clarify.
Line 64: A key citation is missing: Xu et al. Environ. Sci. Technol., 2024. (DOI:10.1021/acs.estlett.4c00451) This paper is a critical study providing evidence for inorganic sulfate formation from OH-initiated decomposition of IEPOX-OS referenced earlier in the text. This should also be discussed in Section 3.2 (line 207).
Line 88: If aliquots were removed at a specific time interval for analysis, this should be specified, as well as whether they were diluted prior to analysis with UPLC.
Line 163: Please quantify the “high reactivity” of aromatic OSs compared with alkyl OSs, citing specific examples of rate constants.
Line 170: The reported errors should be specified as calculated from the regression fit. It is unclear whether repeats were performed and propagated to yield this value.
Line 179: What are the ionic strengths of the solutions in your reactor at pH 3 and pH 8? Please calculate (using approximations as needed) to provide a reference for the difference in ionic strength that could be affecting kinetics.
Section 3.2: Results from LC-MS analysis of dark experiments should be included to eliminate the possibility that any reported products are analytical artifacts.
Line 200: Please clarify that this work does not disprove isoprene as a source of this m/z 139, but rather this work provides an additional source.
Section 3.2: Since conversion of OSs to inorganic sulfate is purported as a main finding of this paper in the abstract (line 15), evidence supporting this should be high-quality enough to include in the main text.
Line 212: The observed peak for m/z 97 is discussed multiple times in this section, but there is no figure showing a mass spectrum with this peak. It is also very important to show that this is not an artifact of the mass spectrometric analysis or a fragment ion. A mass spectrum from a dark/0 min/standard sample showing the absence (or extremely low signal) of m/z 97 is important to demonstrate this. The extracted ion chromatogram (EIC) for m/z 97 should also be compared with the EICs of identified organosulfate products (such as those listed in Table S1 for phenyl sulfate) to see if their peaks align, as this would suggest fragmentation in the MS to form m/z 97.
Line 224: There is no discussion of inorganic sulfate quantification using ion chromatography, and thus a mass yield is very confusing to report. With all the uncertainties related to the inorganic sulfate peak in the chromatogram, this should not be included in the manuscript.
Line 225: The peak of inorganic sulfate does not appear negligible based on Figure S6 – please provide the chromatogram from a blank/dark/0 min sample to support this claim. This is especially important since it is claimed earlier that the existence of a m/z 97 peak in mass spectra implies conversion of OSs to inorganic sulfate. If small amounts of sulfate are detected with IC without OH oxidation, m/z 97 is likely to appear in the mass spectrum at 0 min as well.
Line 237: The products from the two other OSs in this study are glossed over very quickly here. Please report relevant mass spectrometry results to support these claims, including molecular formulas similarly to Table S2. If this is not possible, then this discussion should not be included and the section should be reframed to ONLY discuss phenyl sulfate.
Two key datasets are missing to support the claims of this paper: (1) mass spectrometry characterization of OH oxidation products from p-tolyl sulfate and 4-ethylphenyl sulfate and (2) ion chromatography data showing formation of inorganic sulfate OH oxidation of p-tolyl sulfate and 4-ethylphenyl sulfate. If these cannot be included, then the scope of claims in the abstract should be narrowed. In its current form, there is only evidence of phenyl sulfate conversion to inorganic sulfate, not multiple aromatic OSs (line 15). Additionally, the characterization of multiphase OH oxidation products of only phenyl sulfate is shown, not multiple aromatic OSs (line 13).
Section 3.3: Throughout this section, differing absorbance/fluorescence is justified with speculations about chemical composition without evidence. This includes speculations about the formation of oligomers/HULIS (line 254, 274) and products with more expanded conjugated systems (line 271), as well as changes in the products formed at different pH (line 291). These claims should be supported with UPLC/LC-MS/MS data, which they have collected for these experiments. It is not sufficient to reference other publications, especially when these compounds should be observable with the analytical technique used.
Technical corrections
Multiple instances where “Oss” rather than “OSs” was used to refer to organosulfates in the text, please double check all abbreviations.
Line 67: There is no reference to Gweme and Styler, although it is the “recent study” discussed through the end of the paragraph.
Line 74: It is unclear why He et al., 2022 is cited here – please clarify.
Line 118: Were these products quantified using IC?
Line 122: “ocus” should be “Focus”?
Line 134: “em” and “ex” should be subscripted.
Line 150: Superscript is missing from scientific notation.
Line 153: Reference to Table 1 is missing.
Table S2 does not specify that these results are for pH 3, as mentioned in the main text (Line 187). Additionally, negative charges are missing from all molecular formulas in the table, although they are included when referenced in the main text.
Colors in Figure S5 are difficult to distinguish from each other.
Citation: https://doi.org/10.5194/egusphere-2025-5606-RC2 - AC3: 'Reply on RC2', Liubin Huang, 27 Feb 2026
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RC3: 'Comment on egusphere-2025-5606', Anonymous Referee #3, 06 Jan 2026
The article by Yang et al. investigates the kinetics and products of liquid-phase OH radical oxidation of three aromatic organosulfates (OSs), namely phenyl sulfate, p-tolyl sulfate, and 4-ethylphenyl sulfate. The authors employed a batch reactor containing an aqueous solution of aromatic OSs, H₂O₂, and dissolved O₂ under xenon lamp irradiation to study OH radical oxidation processes. Concentrations of the OSs were quantified using LC–MS analysis, while UV–visible absorption and fluorescence spectra were also measured. The results and conclusions provide new insights into this field, including faster OH oxidation rates under more alkaline conditions, the formation of inorganic sulfate, and the production of brown carbon–like species. Incorporation of these findings into atmospheric models could improve understanding of the atmospheric impacts of aromatic OS oxidation. However, the manuscript would benefit from additional work and refinement prior to publication in an EGU journal, particularly through the inclusion of missing references, more detailed discussion of the results, and a clearer overall structure.
Major Revisions：
1）Change “multiphase” to “liquid-phase” or delete “multiphase” from the title, the whole manuscript and supplement. In atmospheric science, the “multiphase reaction” generally means heterogeneous reactions happening between different phases (e.g., gas and liquid). To study multiphase reactions, people generally react gas-phase VOCs or oxidants with liquid-phase aerosol inside a chamber. All papers with titles including “multiphase” the authors cited used a chamber to study the aerosol-gas reaction. This study used a water solution containing reactants in batch reactor and studied liquid-phase reactions.
2）In Section 2.3, explain in more detail the quantification of OSs compounds and do a mass closure calculation. The authors said that the concentration was detected by LCMS analysis. However, the specific quantification process was unclear in the paper. Two essential questions the reader may ask: What standards the authors used to quantify OSs and their oxidation products? What percentage of total compounds quantified using both IC and LC/MS (a mass closure calculation)?
3) The authors observed that aromatic OSs reacting with OH radical more rapidly in alkaline solution (pH 8) compared to acidic solution (pH 3). However, I am not entirely convinced that the acidity is the reason for this change in OH oxidation kinetics. As the solution at pH 3 contains HCl and the solution at pH 8 contains phosphate buffer (Na2HPO4 and NaH2PO4). These additional compounds in solutions may affect the OH radical oxidation kinetics. The authors need to prove that the change in oxidation kinetics is indeed caused by acidity change. The authors also need to explain why they chose phosphate buffer to adjust the pH, as phosphate is not a ubiquitous species in atmosphere.
3) Add a section specifically explaining the calculation of the lifetime of OSs against OH radical oxidation. The authors could include more information on the ambient OH concentrations. Ambient OH concentrations [•OH] could fluctuate greatly from remote to urban environments, the authors could discuss a little more about the ambient OH concentrations across different regions, especially on the urban sites. Moreover, in Lines 298-299, the authors mentioned that “The lifetime of aromatic OSs is significantly shorter than those of aliphatic OSs (Gweme and Styler, 2024; Lai et al., 2025).” However, the authors didn’t further explain why. Also, the cited studies reported oxidation kinetics in liquid-phase. There are other laboratory studies (listed below) reported the heterogeneous OH oxidation kinetics of aliphatic OSs. The authors may also want to include these studies in the discussion of aerosol lifetimes.
a. Yan, J.; Zhang,Y.; Chen,Y.; Armstrong, N.C.; Buchenau, N. A.; Lei, Z.; Xiao,Y.; Zhang, Z.; Lambe, A. T.; Chan,M.N. Kinetics and Products of Heterogeneous Hydroxyl Radical Oxidation of Isoprene Epoxydiol-Derived Secondary Organic Aerosol. ACS Earth Space Chem. 2023, 7, 1916.
b. Yan, Jin, N. Cazimir Armstrong, Katherine R. Kolozsvari, et al. “Effect of Initial Seed Aerosol Acidity on the Kinetics and Products of Heterogeneous Hydroxyl Radical Oxidation of Isoprene Epoxydiol-Derived Secondary Organic Aerosol.” The Journal of Physical Chemistry A 129, no. 18 (2025): 4132–47. https://doi.org/10.1021/acs.jpca.4c08082.
c. Chen, Yuzhi, Yue Zhang, Andrew T. Lambe, et al. “Heterogeneous Hydroxyl Radical Oxidation of Isoprene-Epoxydiol-Derived Methyltetrol Sulfates: Plausible Formation Mechanisms of Previously Unexplained Organosulfates in Ambient Fine Aerosols.” Environmental Science & Technology Letters 7, no. 7 (2020): 460–68. https://doi.org/10.1021/acs.estlett.0c00276.
d. Lam, H. K., Kwong, K. C., Poon, H. Y., Davies, J. F., Zhang, Z., Gold, A., Surratt, J. D., and Chan, M. N.: Heterogeneous OH oxidation of isoprene-epoxydiol-derived organosulfates: kinetics, chemistry and formation of inorganic sulfate, Atmos. Chem. Phys., 19, 2433–2440, https://doi.org/10.5194/acp-19-2433-2019, 2019.
Minor Comments:
1) The first row of the Table S3 lists the concentration of OH radicals while other rows list the lifetimes (days). It would be better to put the concentration of OH radicals as a note at the end of the table or on the title.
2) Lines 21-25: Cite study Hu, W. W., P. Campuzano-Jost, B. B. Palm, et al. “Characterization of a Real-Time Tracer for Isoprene Epoxydiols-Derived Secondary Organic Aerosol (IEPOX-SOA) from Aerosol Mass Spectrometer Measurements.” Atmospheric Chemistry and Physics 15, no. 20 (2015): 11807–33. https://doi.org/10.5194/acp-15-11807-2015.
3) Lines 34-35: The focus of the study is on the aromatic OSs, I would suggest the authors focus more on the introduction of aromatic OSs in urban sites. The authors could lists more studies which detected aromatic OSs in the urban atmosphere (Huang et al.,2020; Li et al., 2023). Then mention the Ma et al., 2025 study to show their contributions to ambient aerosol.
a. Huang, Liubin, Tongshan Liu, and Vicki H. Grassian. Radical-Initiated Formation of Aromatic Organosulfates and Sulfonates in the Aqueous Phase. Environmental Science & Technology 54, no. 19 (2020): 11857–64. https://doi.org/10.1021/acs.est.0c05644.
b. Li, Ailin, Xiaodi Shi, Xinghua Qiu, et al. “Organosulfur Compounds in Ambient Fine Particulate Matter in an Urban Region: Findings of a Nontargeted Approach.” Science of The Total Environment 887 (August 2023): 164114. https://doi.org/10.1016/j.scitotenv.2023.164114.
4) Lines 41-42: Add references to “previous studies revealed that the addition of sulfate radicals on the C=C bond can result in the formation of OSs in aqueous aerosols”.
5) Lines 54-55: I don’t see the point of stating the effects of carbon chain length on the OH oxidation kinetics in the introduction part, as the authors later explains the chain length effects in Section 3.1. So I would recommend the authors to just summarize the oxidation kinetics reported from previous studies for aliphatic OSs in introduction part.
6) Line 67. The author mentioned that “a very recent study…”. However there is no reference to this study.
7) Lines 72-74: The sentence “In this study, we investigated the multiphase reaction of atmospherically relevant aromatic OSs (i.e., phenyl sulfate, p-tolyl sulfate, and 4-ethylphenyl sulfate) with OH radicals (He et al., 2022)” is somewhat confusing, as the reference (Hu et al., 2022) appears to support the present study rather than the atmospheric relevance of the compounds. I suggest separating this into two sentences. For example, the authors could write: “Phenyl sulfate, p-tolyl sulfate, and 4-ethylphenyl sulfate have been observed as atmospherically relevant aromatic OSs in Chengdu, an urban environment during winter (He et al., 2022). In this study, we investigated their liquid-phase reactions with OH radicals.”
8) Lines 85-86: add reference Pye et al., 2020 review paper on aerosol acidity, focus more on the aerosol in the urban sites.
a. Pye, Havala O. T., Athanasios Nenes, Becky Alexander, et al. “The Acidity of Atmospheric Particles and Clouds.” Atmospheric Chemistry and Physics 20, no. 8 (2020): 4809–88. https://doi.org/10.5194/acp-20-4809-2020.
9) Line 88: the authors could explain more why choose the initial concentration of aromatic OSs to be 0.05 mM? How is this value compared to that in ambient aerosol?
10) Lines 89-90: “additional experiments with elevated concentrations of OSs (0.5 or 1 mM) were carried out in order to observe obvious product signals and optical change characteristics.” Does the high concentration of OSs change the oxidation kinetics determined using lower concentration (0.05mM)? The authors could report both the oxidation kinetics (k) for low and high concentration experiments if possible.
11) Lines 154-155: I recommend the authors also cite following laboratory studies (listed below) on the heterogeneous OH radical oxidation of isoprene epoxy diol-derived secondary organic aerosol (IEPOX-SOA). These two studies also suggest that reaction rate is faster for aliphatic OSs with longer carbon chain length:
a. Yan, J.; Zhang,Y.; Chen,Y.; Armstrong, N.C.; Buchenau, N. A.; Lei, Z.; Xiao,Y.; Zhang, Z.; Lambe, A. T.; Chan,M.N. Kinetics and Products of Heterogeneous Hydroxyl Radical Oxidation of Isoprene Epoxydiol-Derived Secondary Organic Aerosol. ACS Earth Space Chem. 2023, 7, 1916.
b. Armstrong, N. C.; Chen, Y.; Cui, T.; Zhang,Y.; Christensen, C.; Zhang, Z.; Turpin, B. J.; Chan, M. N.; Gold, A.; Ault, A. P. Isoprene Epoxydiol-Derived Sulfated and Nonsulfated Oligomers Suppress Particulate Mass Loss during Oxidative Aging of Secondary Organic Aerosol. Environ. Sci.Technol. 2022, 56, 16611.
12) Lines 207-208: add references to the “previous studies”.
13) Line 212: change “sulfate anions (•SO4–)” to “sulfate radical anions (•SO4–)” assuming the “•” means “Radicals”.
14) Lines 222-224: add references on “benzoic acid can undergo decarboxylation reactions”, and “the elimination of the sulfate group from phenyl sulfate”.
15) Lines 230-231: the author wrote “Figure S7 reveals that C6H5O5S– exists as three isomeric forms: ortho, meta, and para hydroxyphenyl sulfate, exhibiting distinct distribution patterns at different pH values.” However, Figure S7 only shows the abundance peak of C6H5O5S– including all structures proposed in Figure 2 mechanism. Figure S7 can only tell us that the OH oxidation happened much faster in alkaline environment (pH 8) compared to more acidic environment (pH 3). I suggest the author don’t mention the three isomeric forms, and reword the sentence.
16) Line 304: In ambient air, a compound with “shorter lifetime” generally considered not as important as the “long lifetime” species regarding their climate impacts. You could reword this to be “the high abundance of aromatic OSs and their fast reactivity with OH radicals in urban environments further underscores their potentially significant role…”
17) In section 4, the author didn’t mention the formation of sulfate anions, which is directly related to the sulfur cycle.
Citation: https://doi.org/10.5194/egusphere-2025-5606-RC3 - AC1: 'Reply on RC3', Liubin Huang, 27 Feb 2026
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2025-5606', Anonymous Referee #1, 13 Dec 2025
Yang et al. investigated the multiphase reaction of aromatic organosulfates with OH radicals, providing pH dependent rate constants, organosulfate products, and produced inorganic sulfate. The authors additionally show evidence for increased absorbance in OS reaction products. The main kinetically related goals of this manuscript are closely related to that of Gweme and Styler (2024) (referenced by the authors). And indeed, these authors find good agreement between their kinetic results and those from Gweme and Styler (2024). But at least as worded in the introduction, the authors suggest that the novelty and necessity of their new study here is to investigate the possibility of inorganic sulfate as a product (something Gweme and Styler did not provide evidence for, at least for aromatic organosulfates). I have concerns about the experimental design and quality control related to their observation of inorganic sulfate as described below. Recent work from their own institution on inorganic sulfate products is also not referenced (https://acp.copernicus.org/articles/25/8575/2025/). I have listed my concerns below, which largely pertain to novelty and need for increased experimental evidence in some cases. Overall, I believe that my concerns should be addressed before I can recommend publication.
Line 35-36: This statement is unsupported and too speculative for an introduction.
Line 51: No need to say ‘potential’ – Hydrolysis is indeed known to removed OSs.
Line 54: …radicals that reacted…
Line 57: “border kind” is at least an unfamiliar term to me, consider using something else
Line 63: “… the partial of OSs…” is confusing as written
Lines 65 – 70: No reference is given for this. Please correct, as the authors seem to use this evidence as the paramount motivation for their study here. Presumably this is Gweme and Styler (2024), but it isn’t confirmed.
Line 88: Is this a summed concentration? Or for each individual component?
Line 96 – 97: This statement needs experimental or referenced support. Even though I appreciate that hydrolysis of aromatic organosulfates is slow, it is critical that the authors make it defensible beyond doubt that hydrolysis isn’t a kinetically meaningful contributor to their aqueous phase analyses.
Line 122: Change ‘spectrometry’ to ‘spectrometer’
Line 150: Missing superscript formatting
Line 196: Typo for ‘radical’
Line 202-203: This is more interesting to me than the motivation that was framed in the introduction
Line 213: Did the authors conduct any full scan mass spectrometry acquisitions of individual organosulfate standards? The detection of m/z 97 does not exclusively indicate inorganic sulfate, as it may also be the result of in-source fragmentation of their organosulfate standards. While electrospray ionization is soft, is still doesn’t eliminate the possibility of such byproduct fragments formed from organic precursors. This needs to be clarified in detail.
Line 225 – 227: If the authors cannot adequately defend their observations (especially for a chemical product that is so important to their studies motivations and novelty), then it should not be included in the manuscript.
Line 228: I’m not sure this is true as written. Again, I need to see more quality control experiments of the standards themselves to be sure of what the exact origin is of the author’s inorganic sulfate peak.
Line 243 – 244: This is vague and unspecific. Statements such as this are best introduced in the introduction with referenced support.
Line 250: This is just my opinion, but descriptors like ‘remarkable’ don’t offer much for a scientific observation. What exactly makes it ‘remarkable?’
Section 3.3: The authors talk about the formation of brown carbon species. They do not provide molecular-level data to better defend this observation despite having the capability to do so (i.e., a high-resolution mass spectrometry system). There are indeed interesting and exciting observations reported in this paragraph. But while they do have the absorbance data, some molecular-level evaluation of these formed compounds would be much more convincing and comprehensive to defend/prove these observations. This type of data, if acquired, should then also be featured in a key manuscript figure.
Figure 4: Please be more descriptive (i.e., avoid acronyms) whenever possible in figure captions and axes. While I hope that most don’t just look at figures, many inevitably do, so it is best to avoid acronyms as much as possible.
Citation: https://doi.org/10.5194/egusphere-2025-5606-RC1 - AC2: 'Reply on RC1', Liubin Huang, 27 Feb 2026
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RC2: 'Comment on egusphere-2025-5606', Anonymous Referee #2, 19 Dec 2025
This manuscript provides evidence that OH oxidation of phenyl sulfate can regenerate inorganic sulfate, and that OH oxidation of aromatic OSs can form BrC products. These are important scientific questions relevant to this journal; however, many claims are made without data to back them despite it being collected. Most notably, products detected with mass spectrometry are only reported for 1 of 5 experiments for which UPLC/LC-MS/MS data was obtained, and ion chromatography data is also only provided for 1 experiment.
I found numerous (>20) grammatical and syntactical errors, and thus I recommend that the authors review the language with a more critical eye and double check their revisions with a grammar checking software. Awkward transition word choices obscured the meaning of many sentences, particularly in the introduction and results & discussion.
Overall, I have many significant concerns about the quality control and experimental methods that need to be addressed before I can recommend this manuscript for publication.
Specific comments
Line 24: It is inaccurate to state that organosulfates constitute “~30% of particulate organic mass,” please rephrase as “up to 30%” or cite specific regions where this mass concentration was measured.
Line 31: “except for isoprene and monoterpenes derived OSs” – confusing wording; were these OSs also detected? Please clarify.
Line 64: A key citation is missing: Xu et al. Environ. Sci. Technol., 2024. (DOI:10.1021/acs.estlett.4c00451) This paper is a critical study providing evidence for inorganic sulfate formation from OH-initiated decomposition of IEPOX-OS referenced earlier in the text. This should also be discussed in Section 3.2 (line 207).
Line 88: If aliquots were removed at a specific time interval for analysis, this should be specified, as well as whether they were diluted prior to analysis with UPLC.
Line 163: Please quantify the “high reactivity” of aromatic OSs compared with alkyl OSs, citing specific examples of rate constants.
Line 170: The reported errors should be specified as calculated from the regression fit. It is unclear whether repeats were performed and propagated to yield this value.
Line 179: What are the ionic strengths of the solutions in your reactor at pH 3 and pH 8? Please calculate (using approximations as needed) to provide a reference for the difference in ionic strength that could be affecting kinetics.
Section 3.2: Results from LC-MS analysis of dark experiments should be included to eliminate the possibility that any reported products are analytical artifacts.
Line 200: Please clarify that this work does not disprove isoprene as a source of this m/z 139, but rather this work provides an additional source.
Section 3.2: Since conversion of OSs to inorganic sulfate is purported as a main finding of this paper in the abstract (line 15), evidence supporting this should be high-quality enough to include in the main text.
Line 212: The observed peak for m/z 97 is discussed multiple times in this section, but there is no figure showing a mass spectrum with this peak. It is also very important to show that this is not an artifact of the mass spectrometric analysis or a fragment ion. A mass spectrum from a dark/0 min/standard sample showing the absence (or extremely low signal) of m/z 97 is important to demonstrate this. The extracted ion chromatogram (EIC) for m/z 97 should also be compared with the EICs of identified organosulfate products (such as those listed in Table S1 for phenyl sulfate) to see if their peaks align, as this would suggest fragmentation in the MS to form m/z 97.
Line 224: There is no discussion of inorganic sulfate quantification using ion chromatography, and thus a mass yield is very confusing to report. With all the uncertainties related to the inorganic sulfate peak in the chromatogram, this should not be included in the manuscript.
Line 225: The peak of inorganic sulfate does not appear negligible based on Figure S6 – please provide the chromatogram from a blank/dark/0 min sample to support this claim. This is especially important since it is claimed earlier that the existence of a m/z 97 peak in mass spectra implies conversion of OSs to inorganic sulfate. If small amounts of sulfate are detected with IC without OH oxidation, m/z 97 is likely to appear in the mass spectrum at 0 min as well.
Line 237: The products from the two other OSs in this study are glossed over very quickly here. Please report relevant mass spectrometry results to support these claims, including molecular formulas similarly to Table S2. If this is not possible, then this discussion should not be included and the section should be reframed to ONLY discuss phenyl sulfate.
Two key datasets are missing to support the claims of this paper: (1) mass spectrometry characterization of OH oxidation products from p-tolyl sulfate and 4-ethylphenyl sulfate and (2) ion chromatography data showing formation of inorganic sulfate OH oxidation of p-tolyl sulfate and 4-ethylphenyl sulfate. If these cannot be included, then the scope of claims in the abstract should be narrowed. In its current form, there is only evidence of phenyl sulfate conversion to inorganic sulfate, not multiple aromatic OSs (line 15). Additionally, the characterization of multiphase OH oxidation products of only phenyl sulfate is shown, not multiple aromatic OSs (line 13).
Section 3.3: Throughout this section, differing absorbance/fluorescence is justified with speculations about chemical composition without evidence. This includes speculations about the formation of oligomers/HULIS (line 254, 274) and products with more expanded conjugated systems (line 271), as well as changes in the products formed at different pH (line 291). These claims should be supported with UPLC/LC-MS/MS data, which they have collected for these experiments. It is not sufficient to reference other publications, especially when these compounds should be observable with the analytical technique used.
Technical corrections
Multiple instances where “Oss” rather than “OSs” was used to refer to organosulfates in the text, please double check all abbreviations.
Line 67: There is no reference to Gweme and Styler, although it is the “recent study” discussed through the end of the paragraph.
Line 74: It is unclear why He et al., 2022 is cited here – please clarify.
Line 118: Were these products quantified using IC?
Line 122: “ocus” should be “Focus”?
Line 134: “em” and “ex” should be subscripted.
Line 150: Superscript is missing from scientific notation.
Line 153: Reference to Table 1 is missing.
Table S2 does not specify that these results are for pH 3, as mentioned in the main text (Line 187). Additionally, negative charges are missing from all molecular formulas in the table, although they are included when referenced in the main text.
Colors in Figure S5 are difficult to distinguish from each other.
Citation: https://doi.org/10.5194/egusphere-2025-5606-RC2 - AC3: 'Reply on RC2', Liubin Huang, 27 Feb 2026
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RC3: 'Comment on egusphere-2025-5606', Anonymous Referee #3, 06 Jan 2026
The article by Yang et al. investigates the kinetics and products of liquid-phase OH radical oxidation of three aromatic organosulfates (OSs), namely phenyl sulfate, p-tolyl sulfate, and 4-ethylphenyl sulfate. The authors employed a batch reactor containing an aqueous solution of aromatic OSs, H₂O₂, and dissolved O₂ under xenon lamp irradiation to study OH radical oxidation processes. Concentrations of the OSs were quantified using LC–MS analysis, while UV–visible absorption and fluorescence spectra were also measured. The results and conclusions provide new insights into this field, including faster OH oxidation rates under more alkaline conditions, the formation of inorganic sulfate, and the production of brown carbon–like species. Incorporation of these findings into atmospheric models could improve understanding of the atmospheric impacts of aromatic OS oxidation. However, the manuscript would benefit from additional work and refinement prior to publication in an EGU journal, particularly through the inclusion of missing references, more detailed discussion of the results, and a clearer overall structure.
Major Revisions：
1）Change “multiphase” to “liquid-phase” or delete “multiphase” from the title, the whole manuscript and supplement. In atmospheric science, the “multiphase reaction” generally means heterogeneous reactions happening between different phases (e.g., gas and liquid). To study multiphase reactions, people generally react gas-phase VOCs or oxidants with liquid-phase aerosol inside a chamber. All papers with titles including “multiphase” the authors cited used a chamber to study the aerosol-gas reaction. This study used a water solution containing reactants in batch reactor and studied liquid-phase reactions.
2）In Section 2.3, explain in more detail the quantification of OSs compounds and do a mass closure calculation. The authors said that the concentration was detected by LCMS analysis. However, the specific quantification process was unclear in the paper. Two essential questions the reader may ask: What standards the authors used to quantify OSs and their oxidation products? What percentage of total compounds quantified using both IC and LC/MS (a mass closure calculation)?
3) The authors observed that aromatic OSs reacting with OH radical more rapidly in alkaline solution (pH 8) compared to acidic solution (pH 3). However, I am not entirely convinced that the acidity is the reason for this change in OH oxidation kinetics. As the solution at pH 3 contains HCl and the solution at pH 8 contains phosphate buffer (Na2HPO4 and NaH2PO4). These additional compounds in solutions may affect the OH radical oxidation kinetics. The authors need to prove that the change in oxidation kinetics is indeed caused by acidity change. The authors also need to explain why they chose phosphate buffer to adjust the pH, as phosphate is not a ubiquitous species in atmosphere.
3) Add a section specifically explaining the calculation of the lifetime of OSs against OH radical oxidation. The authors could include more information on the ambient OH concentrations. Ambient OH concentrations [•OH] could fluctuate greatly from remote to urban environments, the authors could discuss a little more about the ambient OH concentrations across different regions, especially on the urban sites. Moreover, in Lines 298-299, the authors mentioned that “The lifetime of aromatic OSs is significantly shorter than those of aliphatic OSs (Gweme and Styler, 2024; Lai et al., 2025).” However, the authors didn’t further explain why. Also, the cited studies reported oxidation kinetics in liquid-phase. There are other laboratory studies (listed below) reported the heterogeneous OH oxidation kinetics of aliphatic OSs. The authors may also want to include these studies in the discussion of aerosol lifetimes.
a. Yan, J.; Zhang,Y.; Chen,Y.; Armstrong, N.C.; Buchenau, N. A.; Lei, Z.; Xiao,Y.; Zhang, Z.; Lambe, A. T.; Chan,M.N. Kinetics and Products of Heterogeneous Hydroxyl Radical Oxidation of Isoprene Epoxydiol-Derived Secondary Organic Aerosol. ACS Earth Space Chem. 2023, 7, 1916.
b. Yan, Jin, N. Cazimir Armstrong, Katherine R. Kolozsvari, et al. “Effect of Initial Seed Aerosol Acidity on the Kinetics and Products of Heterogeneous Hydroxyl Radical Oxidation of Isoprene Epoxydiol-Derived Secondary Organic Aerosol.” The Journal of Physical Chemistry A 129, no. 18 (2025): 4132–47. https://doi.org/10.1021/acs.jpca.4c08082.
c. Chen, Yuzhi, Yue Zhang, Andrew T. Lambe, et al. “Heterogeneous Hydroxyl Radical Oxidation of Isoprene-Epoxydiol-Derived Methyltetrol Sulfates: Plausible Formation Mechanisms of Previously Unexplained Organosulfates in Ambient Fine Aerosols.” Environmental Science & Technology Letters 7, no. 7 (2020): 460–68. https://doi.org/10.1021/acs.estlett.0c00276.
d. Lam, H. K., Kwong, K. C., Poon, H. Y., Davies, J. F., Zhang, Z., Gold, A., Surratt, J. D., and Chan, M. N.: Heterogeneous OH oxidation of isoprene-epoxydiol-derived organosulfates: kinetics, chemistry and formation of inorganic sulfate, Atmos. Chem. Phys., 19, 2433–2440, https://doi.org/10.5194/acp-19-2433-2019, 2019.
Minor Comments:
1) The first row of the Table S3 lists the concentration of OH radicals while other rows list the lifetimes (days). It would be better to put the concentration of OH radicals as a note at the end of the table or on the title.
2) Lines 21-25: Cite study Hu, W. W., P. Campuzano-Jost, B. B. Palm, et al. “Characterization of a Real-Time Tracer for Isoprene Epoxydiols-Derived Secondary Organic Aerosol (IEPOX-SOA) from Aerosol Mass Spectrometer Measurements.” Atmospheric Chemistry and Physics 15, no. 20 (2015): 11807–33. https://doi.org/10.5194/acp-15-11807-2015.
3) Lines 34-35: The focus of the study is on the aromatic OSs, I would suggest the authors focus more on the introduction of aromatic OSs in urban sites. The authors could lists more studies which detected aromatic OSs in the urban atmosphere (Huang et al.,2020; Li et al., 2023). Then mention the Ma et al., 2025 study to show their contributions to ambient aerosol.
a. Huang, Liubin, Tongshan Liu, and Vicki H. Grassian. Radical-Initiated Formation of Aromatic Organosulfates and Sulfonates in the Aqueous Phase. Environmental Science & Technology 54, no. 19 (2020): 11857–64. https://doi.org/10.1021/acs.est.0c05644.
b. Li, Ailin, Xiaodi Shi, Xinghua Qiu, et al. “Organosulfur Compounds in Ambient Fine Particulate Matter in an Urban Region: Findings of a Nontargeted Approach.” Science of The Total Environment 887 (August 2023): 164114. https://doi.org/10.1016/j.scitotenv.2023.164114.
4) Lines 41-42: Add references to “previous studies revealed that the addition of sulfate radicals on the C=C bond can result in the formation of OSs in aqueous aerosols”.
5) Lines 54-55: I don’t see the point of stating the effects of carbon chain length on the OH oxidation kinetics in the introduction part, as the authors later explains the chain length effects in Section 3.1. So I would recommend the authors to just summarize the oxidation kinetics reported from previous studies for aliphatic OSs in introduction part.
6) Line 67. The author mentioned that “a very recent study…”. However there is no reference to this study.
7) Lines 72-74: The sentence “In this study, we investigated the multiphase reaction of atmospherically relevant aromatic OSs (i.e., phenyl sulfate, p-tolyl sulfate, and 4-ethylphenyl sulfate) with OH radicals (He et al., 2022)” is somewhat confusing, as the reference (Hu et al., 2022) appears to support the present study rather than the atmospheric relevance of the compounds. I suggest separating this into two sentences. For example, the authors could write: “Phenyl sulfate, p-tolyl sulfate, and 4-ethylphenyl sulfate have been observed as atmospherically relevant aromatic OSs in Chengdu, an urban environment during winter (He et al., 2022). In this study, we investigated their liquid-phase reactions with OH radicals.”
8) Lines 85-86: add reference Pye et al., 2020 review paper on aerosol acidity, focus more on the aerosol in the urban sites.
a. Pye, Havala O. T., Athanasios Nenes, Becky Alexander, et al. “The Acidity of Atmospheric Particles and Clouds.” Atmospheric Chemistry and Physics 20, no. 8 (2020): 4809–88. https://doi.org/10.5194/acp-20-4809-2020.
9) Line 88: the authors could explain more why choose the initial concentration of aromatic OSs to be 0.05 mM? How is this value compared to that in ambient aerosol?
10) Lines 89-90: “additional experiments with elevated concentrations of OSs (0.5 or 1 mM) were carried out in order to observe obvious product signals and optical change characteristics.” Does the high concentration of OSs change the oxidation kinetics determined using lower concentration (0.05mM)? The authors could report both the oxidation kinetics (k) for low and high concentration experiments if possible.
11) Lines 154-155: I recommend the authors also cite following laboratory studies (listed below) on the heterogeneous OH radical oxidation of isoprene epoxy diol-derived secondary organic aerosol (IEPOX-SOA). These two studies also suggest that reaction rate is faster for aliphatic OSs with longer carbon chain length:
a. Yan, J.; Zhang,Y.; Chen,Y.; Armstrong, N.C.; Buchenau, N. A.; Lei, Z.; Xiao,Y.; Zhang, Z.; Lambe, A. T.; Chan,M.N. Kinetics and Products of Heterogeneous Hydroxyl Radical Oxidation of Isoprene Epoxydiol-Derived Secondary Organic Aerosol. ACS Earth Space Chem. 2023, 7, 1916.
b. Armstrong, N. C.; Chen, Y.; Cui, T.; Zhang,Y.; Christensen, C.; Zhang, Z.; Turpin, B. J.; Chan, M. N.; Gold, A.; Ault, A. P. Isoprene Epoxydiol-Derived Sulfated and Nonsulfated Oligomers Suppress Particulate Mass Loss during Oxidative Aging of Secondary Organic Aerosol. Environ. Sci.Technol. 2022, 56, 16611.
12) Lines 207-208: add references to the “previous studies”.
13) Line 212: change “sulfate anions (•SO4–)” to “sulfate radical anions (•SO4–)” assuming the “•” means “Radicals”.
14) Lines 222-224: add references on “benzoic acid can undergo decarboxylation reactions”, and “the elimination of the sulfate group from phenyl sulfate”.
15) Lines 230-231: the author wrote “Figure S7 reveals that C6H5O5S– exists as three isomeric forms: ortho, meta, and para hydroxyphenyl sulfate, exhibiting distinct distribution patterns at different pH values.” However, Figure S7 only shows the abundance peak of C6H5O5S– including all structures proposed in Figure 2 mechanism. Figure S7 can only tell us that the OH oxidation happened much faster in alkaline environment (pH 8) compared to more acidic environment (pH 3). I suggest the author don’t mention the three isomeric forms, and reword the sentence.
16) Line 304: In ambient air, a compound with “shorter lifetime” generally considered not as important as the “long lifetime” species regarding their climate impacts. You could reword this to be “the high abundance of aromatic OSs and their fast reactivity with OH radicals in urban environments further underscores their potentially significant role…”
17) In section 4, the author didn’t mention the formation of sulfate anions, which is directly related to the sulfur cycle.
Citation: https://doi.org/10.5194/egusphere-2025-5606-RC3 - AC1: 'Reply on RC3', Liubin Huang, 27 Feb 2026
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Yu Yang
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The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
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Yang et al. investigated the multiphase reaction of aromatic organosulfates with OH radicals, providing pH dependent rate constants, organosulfate products, and produced inorganic sulfate. The authors additionally show evidence for increased absorbance in OS reaction products. The main kinetically related goals of this manuscript are closely related to that of Gweme and Styler (2024) (referenced by the authors). And indeed, these authors find good agreement between their kinetic results and those from Gweme and Styler (2024). But at least as worded in the introduction, the authors suggest that the novelty and necessity of their new study here is to investigate the possibility of inorganic sulfate as a product (something Gweme and Styler did not provide evidence for, at least for aromatic organosulfates). I have concerns about the experimental design and quality control related to their observation of inorganic sulfate as described below. Recent work from their own institution on inorganic sulfate products is also not referenced (https://acp.copernicus.org/articles/25/8575/2025/). I have listed my concerns below, which largely pertain to novelty and need for increased experimental evidence in some cases. Overall, I believe that my concerns should be addressed before I can recommend publication.
Line 35-36: This statement is unsupported and too speculative for an introduction.
Line 51: No need to say ‘potential’ – Hydrolysis is indeed known to removed OSs.
Line 54: …radicals that reacted…
Line 57: “border kind” is at least an unfamiliar term to me, consider using something else
Line 63: “… the partial of OSs…” is confusing as written
Lines 65 – 70: No reference is given for this. Please correct, as the authors seem to use this evidence as the paramount motivation for their study here. Presumably this is Gweme and Styler (2024), but it isn’t confirmed.
Line 88: Is this a summed concentration? Or for each individual component?
Line 96 – 97: This statement needs experimental or referenced support. Even though I appreciate that hydrolysis of aromatic organosulfates is slow, it is critical that the authors make it defensible beyond doubt that hydrolysis isn’t a kinetically meaningful contributor to their aqueous phase analyses.
Line 122: Change ‘spectrometry’ to ‘spectrometer’
Line 150: Missing superscript formatting
Line 196: Typo for ‘radical’
Line 202-203: This is more interesting to me than the motivation that was framed in the introduction
Line 213: Did the authors conduct any full scan mass spectrometry acquisitions of individual organosulfate standards? The detection of m/z 97 does not exclusively indicate inorganic sulfate, as it may also be the result of in-source fragmentation of their organosulfate standards. While electrospray ionization is soft, is still doesn’t eliminate the possibility of such byproduct fragments formed from organic precursors. This needs to be clarified in detail.
Line 225 – 227: If the authors cannot adequately defend their observations (especially for a chemical product that is so important to their studies motivations and novelty), then it should not be included in the manuscript.
Line 228: I’m not sure this is true as written. Again, I need to see more quality control experiments of the standards themselves to be sure of what the exact origin is of the author’s inorganic sulfate peak.
Line 243 – 244: This is vague and unspecific. Statements such as this are best introduced in the introduction with referenced support.
Line 250: This is just my opinion, but descriptors like ‘remarkable’ don’t offer much for a scientific observation. What exactly makes it ‘remarkable?’
Section 3.3: The authors talk about the formation of brown carbon species. They do not provide molecular-level data to better defend this observation despite having the capability to do so (i.e., a high-resolution mass spectrometry system). There are indeed interesting and exciting observations reported in this paragraph. But while they do have the absorbance data, some molecular-level evaluation of these formed compounds would be much more convincing and comprehensive to defend/prove these observations. This type of data, if acquired, should then also be featured in a key manuscript figure.
Figure 4: Please be more descriptive (i.e., avoid acronyms) whenever possible in figure captions and axes. While I hope that most don’t just look at figures, many inevitably do, so it is best to avoid acronyms as much as possible.