Manuscript egusphere-2026-1720, "DMS, MeSH and nanoparticles in semi-controlled deck-borne experiments using Antarctic seawater: on the effect of UV light", by Chamba et al. All line numbers refer to egusphere-2026-1720-manuscript-version2.pdf.
The paper describes paired incubations of Antarctic seawater in two on-deck Air-Sea Interface Tanks during the POLAR-CHANGE cruise, one under a lid transparent to the whole spectrum and the other under a lid that cuts off wavelengths below about 375 nm. DMS and MeSH fluxes and aqueous concentrations are derived from the headspace measurements, the nanoparticle population of each headspace is followed at the same time, and both are compared with the plankton and viral assemblages sampled inside the tanks. The main results, that removing UV increases DMS fluxes by about a quarter and MeSH fluxes by close to 60%, that the effect is largest at night, and that new particle formation is almost restricted to the tank without UV, are unusual and worth publishing. The paired design is what makes them credible, and experiments A and B, in which the same water was kept for two days, give the biological comparisons something to work with.
I thank the authors for their careful reply and for the revised version of the manuscript. They have answered most of the points I raised in the first round. On the main point, the absence of statistical support for most of the differences reported, the revision goes a good way: figure 5 now carries the fitted relationships with their equation, R2 and p value, which is what was needed and makes the figure much more useful to other groups working in the region, and the comparisons of the MeSH/(DMS+MeSH) ratios and of the N1 concentrations between the two tanks are now supported by paired Wilcoxon signed-rank tests with effect sizes, with the software, the library versions and the testing procedure stated. The new material on the pumping system, on the cytometric detection of the large viruses typical of Southern Ocean waters, on the meaning of Fv/Fm and on polar diatoms as DMSP producers also improves the paper, and I think the decision to drop the regression forced through the origin was the right one.
Little of what is left requires new analysis. Three statements survive in the manuscript that the revised evidence no longer supports, and a set of comparisons is still described as significant with no test attached. See my comments below for details.
Statistical treatment
The tests that were added are done properly, which makes the remaining gaps more visible. First, the description of the statistics at lines 694-697 sits under Code availability, and it would be easier to find as a short subsection of the methods, if not at least place a call in the Code availability so readers know where to look for the statistical details. Second, that description covers the Wilcoxon signed-rank test only, while a Mann-Whitney U test is used at line 352 and in the reply; please describe both, with the reason for choosing a paired or an unpaired test in each case, and give the statistic, the p value and the sample size every time a test is mentioned, as is done correctly at lines 401-403 and 425-426. Third, several of the comparisons across tanks and water types involve many simultaneous tests and no allowance is made for this; a false discovery rate control such as the one proposed by Benjamini and Hochberg (1995) is the least intrusive option and would suit the correlation matrices of figure S8 particularly well. Fourth, comparisons that are still made with no test at all include the water type contrasts of figure 6, the responses of the phytoplankton groups to UV in figures 10 and S.4, the Fv/Fm patterns of figure 11, and the ozone differences at lines 421-422. Some of these may not survive a test, and figure 11 in particular shows boxes that overlap almost completely. Where that happens it is better to describe the pattern as apparent and to say that it is not statistically resolved than to keep the present wording.
Cryptophytes, nanophytoplankton and chlorophyll a
The cryptophyte result has been removed in some places and left in others, so the manuscript now disagrees with itself. The reply explains that the covariation was obtained with DMS and MeSH values that have since been corrected, and figure S8A shows no significant correlation between cryptophyte abundance and either DMSw or MeSHw. The abstract and one discussion paragraph were changed accordingly, but the claim is still made at lines 613-615 and again at lines 668-669, in the conclusions. The sentence at line 450 about cryptophytes responding positively to UV towards the end of the experiments has lost the figure it used to point to, so a reader has no way of checking it. Please either take cryptophytes out of the first two statements or give the coefficients that do apply, and restore a figure call-out for the third.
The claim that nanophytoplankton abundance predicts seawater DMS better than chlorophyll a is now made without any supporting analysis. It appears at lines 625-627 and, in a stronger form, at lines 669-673, where the ratio of DMSw to nanophytoplankton abundance is said to vary less than the ratio to chlorophyll a, a comparison that is shown nowhere in the paper. The analysis that supported it, the former figure 13, has been deleted, and the reply states that the regression is not significant when it is not forced through the origin. I see three ways out. The authors can report the ordinary least squares regression with its intercept, R2 and p value and let readers judge; they can show the ratio comparison described in the conclusions as a figure or a table with the corresponding test; or they can reduce both statements to something the POLAR-CHANGE data are consistent with, mentioning that Rocco et al. (2025a) found the relationship in a different plankton community. Keeping the conclusion after removing the evidence is the one option I would advise against.
The inverse relation between chlorophyll a and the two sulfur volatiles is still not discussed. Figure S8A gives Spearman coefficients of about -0.8 for chlorophyll a against DMSw and -0.67 against MeSHw during the experiments, and two of the phytoplankton size classes behave in the same way. This is an interesting result and it deserves a couple of sentences, particularly because positive chlorophyll a to DMSP relations are commonly found in Antarctic coastal and glacially influenced waters, where the DMSP pool follows biomass while DMS does not (Li et al., 2024; Petrou et al., 2026). A decoupling between DMSP production and DMS accumulation through bacterial demethylation and photochemical loss would be a reasonable frame, and it would connect this result to the aqueous phase reactivity already discussed in section 4.1. The general caveat added at the beginning of section 4.2, that the correlations should be read individually and not as cause and effect, is fair, but it does not replace a discussion of the strongest signal in the correlation matrix of the authors themselves.
Plankton groups that were not measured in the tanks
The material on the micro-phytoplankton community given in the reply is more informative than what reached the manuscript. The reply says that diatoms accounted on average for less than 40% of the micro-phytoplankton carbon while dinoflagellates accounted for more than 60%, and that the cruise probably took place during a diatom post-bloom, which would make dinoflagellates the likely dominant DMSP source in the tanks. That is a substantive argument and it belongs in the paper. The methods paragraph at lines 243-248 describes the Utermöhl analysis but gives none of its results, and the discussion still contains no statement of the limitation, namely that micro-phytoplankton was characterised in the underway samples and not inside the ASITs, so that the biological comparisons reported here concern the pico- and nanophytoplankton fractions only. A short paragraph in section 4.2 would settle this, and the wording of the abstract and of the conclusions should follow.
Derived concentrations and figure S8
The rewritten text at lines 194-206, explaining how the departures from equilibrium of 2.6 and 7.2 were obtained, is a clear improvement and was worth doing. Since every correlation in section 4.2 and in figure 12 uses DMSw and MeSHw calculated from headspace mole fractions rather than measured in the tanks, one sentence acknowledging that the uncertainty of these values is larger than that of a direct measurement, and that figure S7 shows offsets against the underway values at particular times, would set the reader's expectations correctly without weakening the analysis.
Figure S8 carries a good part of the argument and needs a fuller caption: which coefficient is plotted, Spearman judging from the colour bar, the sample size behind each panel, what a blank cell means, the significance threshold used, and whether the p values are adjusted for multiple testing. As things stand a reader cannot tell whether a blank cell means that the correlation was not significant or that it was not computed, and that ambiguity is what produced the contradiction discussed above.
Specific comments
Line 21. "are are of particular interest".
Line 50. Raised in the first round and not addressed: if "the marine atmosphere" means the marine boundary layer here, please say so.
Line 95 and figure 1. The caption now explains that each point is an hourly position of the ship, which helps. My earlier request still stands, though. Since the track crosses itself several times, a supplementary table with the dates and the coordinates of the periods shown would let readers recover what the overlapping symbols hide.
Lines 243-248. The Utermöhl analysis and the carbon conversion are described but no result from them is given, and Rocchi et al. (2025) is cited here without appearing in the reference list.
Line 244. The text cites Edler and Elbrächter (2010) while the reference list gives Karlson et al. (2010) for what seems to be the same IOC manual. Please reconcile the two.
Lines 284 and 286. Crabeck and Rocchi (in press) and Ferracci et al. (2024) are cited but not listed.
Lines 295, 491, 493 and 506. Salignat et al. (in press) is cited four times and the reference list contains only Salignat et al. (2025), which is the WRF-Chem study and a different paper. Please add the missing entry with its status at the time of submission.
Lines 327-333. Also raised in the first round. This passage on why the ASIT fluxes and the ambient air concentrations need not follow one another is interpretation rather than result, and would sit better in section 4.1, where it could be expanded and referenced.
Lines 343-345 and figure 5. The text gives R2 = 0.88 for the Control-ASIT and 0.81 for the noUV-ASIT while the fits now printed in panels A and B give 0.77 and 0.66. Please check which is right and make the two agree. The value quoted at line 514 for Rocco et al. (2025a) should be checked at the same time, since 0.81 also appears there.
Line 352. "significantly different with Mann-Whitney U test". Please give U, the p value and the sample sizes, and say which pairs were compared, since four water types appear in figure 6.
Lines 354-357, caption of figure 6. The caption defines the boxplot conventions but says nothing about testing. If the differences among the four observational periods were tested, the test and the correction for multiple comparisons should appear in the caption; if they were not, the text should not call them significant.
Line 361. "significantly stronger diel contrast in the Control-ASIT", with no test given here. The reply reports p = 0.048 with r = 0.152 for the day to night comparison, which is marginal and has a small effect size. If that is the test behind this sentence, it should be reported with those values and the wording adjusted accordingly.
Lines 390-395, figure 9. Thank you for stating in the caption that panels B and C use different axes. The comparison that still has no test is the one between water types within each tank, which the between-tank test at lines 425-426 does not cover.
Lines 421-422. The ozone differences of 37% and 53% between the two tanks during experiments A and B are given with no test and no measure of variability.
Lines 438-451. The responses of the phytoplankton groups to UV, including the different timing for the 2-7 um and the 7-20 um fractions, are described from figure 10 alone. Given how close the two curves run in several of the panels, these statements need testing before they can be phrased as they are.
Line 450. The claim about cryptophytes responding positively to UV has lost its figure call-out. Please restore it or drop the claim.
Lines 459-470 and figure 11, caption at lines 473-475. The differences in Fv/Fm between the two tanks, and between the tanks and the underway water, are the least convincing of the untested comparisons, since the boxes in figure 11 overlap to a large extent. Please test them, and if they are not resolved say so. The diel pattern itself is clear and does not depend on the between-treatment claim.
Lines 613-615. Cryptophytes should be removed here or the statement supported, as discussed above.
Lines 625-627 and lines 669-673. The nanophytoplankton against chlorophyll a claim, as discussed above.
Lines 668-669. Cryptophytes again, this time in the conclusions.
Line 677. "the increase of airs MeSH concentrations".
Lines 691-697. Please move the description of the statistical analyses to the methods and add the Mann-Whitney U test and any correction for multiple comparisons. Virtanen et al. (2020) is cited at line 694 but not listed.
Supplement. Two different figures are numbered S.5, the cryptophyte time series and the new normalised diel profiles, and the text calls on figure S.5 for both. The supplementary reference list also gives Wohl and Williams twice, as a preprint and as the published ACP paper, and a tracked change note in French has been left in the file.
References
Benjamini, Y. and Hochberg, Y.: Controlling the false discovery rate: a practical and powerful approach to multiple testing. Journal of the Royal Statistical Society B, 57, 289-300, https://doi.org/10.1111/j.2517-6161.1995.tb02031.x, 1995.
Li, C. X., Chen, K., Sun, X., Liu, L., Xin, M., Liu, X. L., and Wang, B. D.: Summer sea ice melting enhances phytoplankton and dimethyl sulfide production. Limnology and Oceanography, 69, 2453-2472, https://doi.org/10.1002/lno.12681, 2024.
Petrou, K., Raina, J. B., Fernandez, E., Ostrowski, M., O'Brien, J., Haydon, T. D., Seymour, J. R., and Nielsen, D. A.: Dimethylsulfoniopropionate and marine microbial associations along an Antarctic glacial-open ocean interface. Limnology and Oceanography, 71, e70290, https://doi.org/10.1002/lno.70290, 2026.
Rocco, M., Dunne, E., Salignat, R., Saint-Macary, A., Peltola, M., Barthelmeß, T., Chamba, G., Barr, N., Safi, K., Marriner, A., Deppeler, S., Rose, C., Uitz, J., Harnwell, J., Engel, A., Colomb, A., Saiz-Lopez, A., Harvey, M. J., Law, C. S., and Sellegri, K.: Relating dimethyl sulphide and methanethiol fluxes to surface biota in the South-West Pacific using shipboard air-sea interface tanks. Journal of Geophysical Research: Atmospheres, 130, e2024JD041072, https://doi.org/10.1029/2024JD041072, 2025.
Virtanen, P., Gommers, R., Oliphant, T. E., Haberland, M., Reddy, T., Cournapeau, D., Burovski, E., Peterson, P., Weckesser, W., Bright, J., and others: SciPy 1.0: fundamental algorithms for scientific computing in Python. Nature Methods, 17, 261-272, https://doi.org/10.1038/s41592-019-0686-2, 2020. |
The manuscript „DMS, MeSH and nanoparticles in semi-controlled deck-borne experiments using Antarctic seawater: on the effect of UV light” from Chamba et al., reports on fluxes of MeSH and DMS during on-deck incubations in so called Air-sea Interaction Tanks (ASITs) and their relation to particle formation. The authors found differences in fluxes using Antarctic waters dependent on UV light availability and furthermore could show that significant new particle formation was only visible when no UV light was available. Seawater concentrations of MeSH and DMS have been calculated from air mixing ratios and are related to biological parameters in order to explain the variability of those gases. The data shows that nanophytoplankton cell counts could better explain DMS variabilities compared to the widely used proxy chl-a.
The presented work shows a clear research idea in order to improve our understanding on the influence of biologically produced trace gases and their air-sea exchange on particle formation in the atmosphere. The manuscript is well structured and most of the time well presented. However, before publication, I would like to address following points.
General comments:
Calculation from atmospheric mixing ratios to oceanic water concentrations.
Could the authors elaborate a bit on the factor 2.6 (deviation from equilibrium) used in eq(3). They refer to data from Rocco et al. (2025a), but it is still unclear where the factor 2.6 is derived from. I understand that the authors derived the factor for MeSH from data shown in Fig.S7 to match the calculated water concentrations from the ASIT with the seawater measurements at the UW outlet from Wohl & Williams et al., (2026). Given that this factor accounts for the deviation from equilibrium I was wondering why MeSH has an almost 3 times stronger factor than DMS?
Links between dissolved gases and microorganisms during experiments.
The authors try very well to explain the links between dissolved gases and microorganisms. However, there are no direct measurement of dissolved trace gases within the ASITs during the experiments. DMS and MeSH are solely calculated based on measured atmospheric mixing ratios. Calculated fluxes (and finally water concentrations) are always in misbalance between water and atmosphere. This is partly accounted for in the calculation of dissolved aqueous concentrations, however, fast changing atmospheric mixing ratios throughout an experiment could overestimate the calculated variability in the aqueous phase. This can particularly be seen in Fig.S7. On Feb 25th DMS air mixing ratios significantly decrease (Fig.3), so do the calculated DMS water concentrations. However, direct measurements from Wohl & Williams et al. (2026) at the underway outlet at the same time show significantly higher concentrations. A similar offset (but vice versa) is visible on March 7th. Furthermore, calculated DMS and MeSH concentrations at the start of ExpB are significantly higher compared to measured water values at the same time. If this discrepancy is potentially induced only through calculation from air-side to water-side values it does not reflect the actual trace gas variability in the water phase of ExpB. Therefore, drawing conclusions from correlating measured biological parameters with calculated trace gas concentrations should be undertaken with care. Moreover, the authors state that they found no strong correlation between aqueous DMS and MeSH and biological parameters during continuous flow which already points to my previous point (when having two continuous flows (water and air) instead of just one).
Specific comments:
Figure 1: It is not clear to me what the points of the cruise track exactly mean. As the distance between the points changes from time to time, I was thinking that each point might be a discrete (or averaged continuous) measurement point. But as no data is shown before Feb 22nd and after March 11th I might be wrong. Please clarify in the figure caption.
l.125. Which kind of seawater pump was used for the water supply? A centrifugal pump e.g. might damage phytoplankton and causes cell lysis which would significantly influence e.g. DMS and MeSH concentrations and subsequent fluxes when monitored in static flow mode in the experiments (e.g. dissolved DMSP conversion to DMS/MeSH). At least the community in he ASITs would not be “natural” anymore.
l.258ff.: All mentioned compounds which show no enrichment in the ASIT headspace are (much) less soluble in seawater compared to MeSH and DMS. Therefore, proposed cold seawater and absence of wind friction should have a stronger influence (dampening) on the gas exchange on MeSH and DMS than on the other gases. Very low oceanic concentrations might be the dominant factor, however, is there any possibility to prove such low concentration with the help of data availability from Wohl & Williams (2026)? With the biological data provided in the manuscript together with a concentration range of seawater DMS of 1-3nM, isoprene (direct product by phytoplankton) should be supersaturated in the water phase which would lead to elevated atmospheric values (at least during the experiments).
Figure 3: Did the authors also measure DMS and MeSH in the ambient line as they did for ozone? As there appears to be a (known) loss of ozone in the long sampling lines (and in the ASIT itself) it would be helpful to rule that out for the other gases. If there are losses as well e.g. in the ASIT this could potentially explain why the authors did not see an increase in atm mixing rations of isoprene, BTEX, etc. Flux from the water to the air and loss in the ASIT itself could cancel each other out. Furthermore, information of kind of particle filters is missing in the manuscript. Might those filters also influence ozone levels downstream if particles (already loaded on filters after some time) react with ozone?
Figure 5: For the fluxes in the noUV Exp A (green crosses) there seems to be a more exponential relation (than linear) which is not visible in the Control ASIT. Did the authors check if this might be a significant difference? This feature is not visible in the relation between atm mixing ratios. Wouldn’t this imply that under no UV conditions atmospheric MeSH reacts faster than DMS whereas with UV the loss rates in the atmosphere are similar?
Figure 7, Figure S3: Diel variations. Did the authors try to normalize the atmospheric mixing ratios (e.g. to the maximum or mean value per day) when checking diel variations? As discussed earlier in the manuscript the absolute concentrations changed significantly dependent on regions (e.g. coastal vs open ocean). This would probably reduce the standard deviation and a potential dial cycle might be more pronounced (visually but also statistically). This technique could also be applied to the radiation data as of now it seems that data is skewed to stronger irradiations in early afternoon.
l.398ff/Figure 9: Do the authors have any explanation why the particle numbers in the noUV-ASIT are lower during each experiment compared to the particle data of the respective region (coastal vs ExpA and open ocean vs ExpB)?
ll.408ff.: It is obvious that chl-a values at the beginning of ExpA are significantly lower (0.5µg/L) than following concentrations (2.0 µg/L) throughout the experiment. Has this sample also been taken from the tap of one of the ASITs or directly at the UW pump outlet? If so, could the location of sampling bias the data? Nanoplankton 15-20µm data show a similar trend (also for ExpB). Furthermore, are chl-a datapoints hidden behind the legend of ExpA or is there no data available for 6am and 12pm?
Fv/Fm ratio: Could there also be mechanistic stress (e.g. pumping shear stress) showing up in the Fv/Fm ratio? It is quite obvious that Fv/Fm is much lower in the beginning of the experiments compared to later stages. According to Fig. 11 UW Fv/Fm ratios are generally lower compared to ASIT ratios. Do the authors also have Fv/Fm data from CTD measurements? This could give valuable insight if microbial community in ASIT is either just less stressed compared to being pumped through hoses, or if microbes are in general less stressed compared to the “real ocean”. If light stress would be the only issue for Fv/Fm ratios, the difference between UW and ASITs should be vice versa due to the different water depths (UW: 4m, ASIT: ~1m).
l.456ff. Aqueous-phase reactivity of DMS. I like the discussion about the potential loss to explain differences in DMS water concentrations in between both ASITs. How about DMS to DMSO oxidation as a potential loss mechanism? Additionally, I was wondering if the authors also considered a potential stronger DMS production in the noUV ASIT compared to the control ASIT. As the authors already pointed out, the difference in between both treatments is strongest during the two experiments. Is there anything known about phytoplankton types around Antarctica with inhibited DMSP production under UV stress?