Hopkins et al. present the production of VOCs from the ozonolysis of natural seawater via controlled laboratory experiments. The study found that VOC production ratios exhibit strong seasonal patterns linked to phytoplankton dynamics, identified fatty acids and algal-derived dissolved organic matter (DOM) as potential key precursors, and provided a preliminary scaling of the process to estimate its global significance. The manuscript is generally well-structured, the methodology is clearly described, and the research addresses an important gap in understanding marine VOC sources. However, I have several concerns on the manuscript that need to be addressed before considering for publication.

Line 14: In the phrase “representativeness of such experiments to the chemically complex”, it is better to revise the word “to” to “for”. 

Line 66: Typo for “quiestcent”.

Line 74: Please delete or revise the word “roughly” as it induces high uncertainties or a weak result.

Line 82-83: It is not clear how the percentage in “(59 % within 3 h, 94 % within 24 h)” represent the samples used in the experiments. 

Line 113: In the O₃ generation methodology, it was mentioned that the O₃ levels were set at 7.7 ± 0.7, 1.7 ± 0.7, and 2.1 ± 1.1 ppmv for spring, summer and winter experiments. These levels are substantially higher than ambient marine O3 levels. In other words, do the experiments have environmental implications and what are the basis for choosing high O₃ levels for the ozonolysis experiments. 

Line 134, Section 2.3: Using the bubble-column system with natural sea water, a significant number of sea-salt particles can be produced. These particles may provide a large surface area for heterogeneous reactions, and may produce VOCs in certain cases. How can the authors assure that the particles will not affect the results of the study? The authors need to clarify and exclude these influences. 

Line 169, Section 3.1: In this work, high concentration of O₃ were used in the experiments. The high concentration of O₃ can react with these VOCs, generating SOA and its intermediate precursors, may also affect the results that the VOCs are from the emission of sea water. How can the authors make sure that the measured VOCs are not secondary produced in the experimental system?  

Line 285, Figure 5: Error bars should be added to the graph.

Line 290, Section 3.3: The laboratory used high concentrations of O₃ (1.7-9 ppmv), while the real environmental concentration was three orders of magnitude lower. This means that if the rate of O₃ dry deposition on the ocean and VOCs emission rate remain unchanged, the amount of VOCs may be significantly reduced at the ambient O₃ levels. I think extrapolating the experimental results to the global ocean is not accurate enough. Furthermore, if the DOM is the key precursor, the uneven distribution of DOM in the global ocean may also affect the VOCs emissions. Therefore, I think this section is unnecessary in the text. Instead, the authors can discuss more on the potential implications of the ozonolysis.

SI, Table S4: What is the limit of detection (LOD) for these VOCs measurements?   

SI, Line 17: Please explain why the VOC peak height was used here is a more appropriate method than the peak area technique?

Summary

Hopkins et al. present new measurements of the production of volatile organic compounds from in the ozonolysis of seawater. This paper sits at the intersection of two poorly constrained areas: that of global ozone deposition to the ocean, a process governed by its reactions at the sea surface with iodide and dissolved organic matter, and the emission of volatile organic compounds produced via ozonolysis. Both processes are challenging to parameterize in chemical transport models, with significant knowledge gaps, including what specific processes regulate the pool of ozone-reactive DOM. A prior, recent publication by this group demonstrated the significant and highly variable contribution organics to total observed ozone deposition to seawater, highlighting that VOC production from that reaction could be of importance. Hopkins et al. build from this, focusing on monitoring the seasonal trends of a few major ozonolysis VOC products and determining their production ratios. These targeted VOCs were tracked in seawater sourced from a single location in the English Channel over the course of 9 non-consecutive months. In the experiment, ozone is bubbled through a whole seawater sample containing an unknown natural mix of DOM. While the bubble column experiment does not perfectly reflect natural ocean turbulence or air-sea interactions, it provides an upper limit similar to that of a highly-aerated white cap regime.

Overall, the paper presents valuable information to the field. However, several points need to be addressed prior to publication.

General Comments:

1) The dataset focuses entirely on VOC production, however a similar experimental setup was used to measure O3 reactivity by this same group. Does this experiment yield direct measurements of O3 reactivity that could be interpreted alongside the VOC production term? Or does the system operate in an ozone–reactant-limited regime, where ozone is consistently fully consumed, thereby preventing meaningful comparison of ozone loss between samples? Along these lines, if VOC production is only a small fraction of O3 loss, where does all of the O3 go? I appreciate that some fraction will react with iodide. Is the rest forming non-volatile VOC? This is an enormous percentage!

2) On line 180-196 the calculation for VOC production is outlined. This is difficult to follow. In part, because it looks like there is a typo in the ozone deposition flux (equation 3). Is that term missing “D”?

3) Ozonolysis of organic material is extremely well studied in organic chemistry. Unfortunately, there is little to no discussion in the paper about chemical mechanisms that link O3 reactions to the select VOC that are suggested as products. Most notable, isoprene. It is nearly impossible to design a reaction mechanism for the production of isoprene from an ozonolysis reaction. This is most likely due to the fact that C5H9+ as measured by the PTR-MS is not isoprene. It has been well established that C5H9+ is formed in PTR through the dehydration of aldehydes (which are dominant ozonolysis products). This was discussed at length in Kilgour et al. 2024, where C5H9+ signal was dominated by the fragmentation of larger aldehydes (not from monoterpenes/sesquiterpenes as Hopkins et al., misreports). This was confirmed by GC-PTR-MS. It would be best if the authors refrained from assigning a molecular structure to the ion. I appreciate the effort to reconstruct “isoprene” from smaller fragments, but those fragments are common to aldehydes as well. Collectively, it seems most likely that the signals measured at C5H9+ are from larger aldehydes and not isoprene. I think the paper still has valuable insight on the production of VOCs, but should be careful in drawing a link between measured ion composition and molecular structure.

It would also be of importance to provide some literature evidence for acetone and acetaldehyde

production from ozonolysis.

4) On line 119-120, the authors note that: “The VOC production vs. ozone input relationship was experimentally determined to be linear at ozone input mixing ratio below ~4 ppmv.” I think the authors need to show this in the SI. This is not intuitive as higher O3 concentrations can lead to a divergent chemical mechanism where radical chemistry is non-linear. If the authors want to extend the results of this study to lower O3 concentrations, this link is essential and should be included in the analysis.

5) It seems that variability in the VOC production ratio is also sensitive to variability in ozone reactions beyond those that make VOC. As stated in the manuscript, ozone loss is not just due to reactions with DOM, as it also reacts with species such as DMS and iodide, present in unknown concentrations in seawater. These reactions also are changing in time, potentially at different rates than those of the DOM. How do you extract the other sources of ozone loss, or is the assumption that ozone loss to other species constant? Would it impact the production ratio if ozone loss to a species like iodide is changing over the course of the experiment? Some fraction of ozone loss term is not due to DOM, and it varies in time. How do you account for the non-DOM reactive component in the fraction of ozone dependent term, FO3? Or is this somehow accounted for in the limits of high O2?

6) Mechanistically, the fatty acid experiment is confusing and the induced confusion does not help to support the goals / aims of the paper. It is already well established that you can make aldehydes from the ozonolysis of unsaturated fatty acids (O3 + oleic acid is one of the most overstudied reactions). More specifically, I don’t understand how a saturated fatty acid reacts with ozone. This gives me a lot of pause. Either the saturated fatty acid is impure or the ozone source is generating other radicals (OH?). In either case, this section is challenging to interpret and does not seem additive to the paper.

7) After reading the paper, the title is a bit misleading “Uncovering precursors for VOC production from ozonolysis of seawater” The title suggests that the paper will be a chemical investigation into the DOM pool composition or what drives it. This paper focuses mostly on the biological levers that regulate the pool as a whole, and then various targeted “checks” to explore if the three key selected VOCs can be produced by different model seawater DOM proxies. The paper also does not complete a statistical analysis of how the precursors relate to VOC production (as discussed in the next comment). It seems like the real advance of the paper is in the long-term measurements and the seasonal trends. Perhaps: “Uncovering the seasonal trends of VOC production from the ozonolysis of seawater” would be a more reflective title.

8) There is no analysis of the Statistical relationship between VOC product yields and chlorophyll or microbial abundance. Figure 2 paints the variability of the biological cycles over the course of seasons, but there is no attempt to directly relate the variables tracked (chlorophyll-a or the

microbial abundance) to the VOC production rates. Including additional statistics or figures (such as a regression of Chl-a and VOC production) would be highly beneficial to support the paper’s claims.

9) It would be helpful to have a bit more of a direct discussion (absolute values) between the VOC production ratios measured here (which are pretty small) to those that have been reported in the literature. The flow reactor approach clearly has a bias toward reactions occurring in the SSML under quiescent periods as noted by Kilgour et al. 2024, which makes it not as representative of open ocean conditions. The bubble column reactor avoids those complications but requires high O3 concentrations. It would be of interest to the reader to help connect these two approaches and the limitations of each.

Specific Comments:

• Line 53: The SML is not always highly enriched in organic matter and surfactants - consider adjusting the language accordingly.
• Section 3.2 uses “VOC-free, aged seawater” (Line 73) as the matrix for all DOM spiking experiments. Did the seawater still contain DOC that was reactive to ozone? Was the same seawater sample used for all VOC precursor experiments, or how was the baseline reactivity subtracted to compare results across samples?
• Line 82: Did you evaluate if there was a significant change in VOC measurements depending on how long after sample collection the experiment was run?
• Line 85-87: This sentence is a bit confusing, particularly due to the placement of “by flow cytometry” in the sentence. Additionally, what technique was used to analyze chlorophyll a? There seems to be a disconnect between the information presented in the methods section and the data shown in Figure 3. Additional context would be useful to know where the different pieces of information in Figure 3c-e come from.
• SI Line 22-23: “Dilutions targeted final cell abundances within ambient seawater ranges (assuming no algal cells in the aged seawater).” What were the concentrations of cell abundances were used in experiments? This seems important to know, should experiments be replicated in the future.
• SI Lines 11-14: DMS purge and oxidation losses. This section is not referenced in the main document. How does this relate to the relevant experiments in the paper?

Minor Points:

• Line 20: “dominant product” should be plural.

• Line 65: “influences these production of VOCs” should be “influences the production of VOCs”

• Lines 56 and 59: Misspelling of artificial as “artifical”

• Line 56: Misspelling of reactions as “reations”

• Line 66: Misspelling of “quiescent” as “quiestcent”

• Line 240: Misspelling of heterogeneous as “heterogenous”

• Hyphenation: Line 25 “ozone driven,” Line 159 “gas tight,” Line 29 “flow through,” Line18 “near surface water”

• Line 59: comma issue? “The majority of these studies used quiescent, artifical or natural seawater with the use of additives to explore potential VOC precursor compounds”

• Line 66-67: oddly phrased with grammatical issues. Consider removing, as the topic is discussed later in the manuscript.

• Line 84: the L in late should be lowercase.

• Line 167: “DOC” is not defined

• Line 106 and SI lines 7-12: inconsistent formatting in equation variables (V compared to Vbub).

• Line 276: the “3” in the unsaturated oleic acid formula should be in the subscript.

• SI Lines 12-13: several instances where something seems to be intended as a subscript: C₍VOC₎, F₍air₎, etc. Would be good to double check formatting.