the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 05 Jun 2026
Identifying biological sources and indicators of surfactants in the sea surface microlayer and subsurface waters using fluorescence and microbial community profiling
Abstract. Marine surfactants accumulate in the sea surface microlayer (SML) where they influence gas transfer velocities and air-sea exchange of climate relevant gases. Despite their importance, the biological sources and reliable proxies of marine surfactants remain poorly constrained. This study paired measurements of surfactant concentrations and fluorescent dissolved organic matter (FDOM) composition with bacterial and protist community profiles in the SML and subsurface waters (SSW) across three hydrographic regions and two seasons in the northwestern Atlantic Ocean. Surfactant concentrations were significantly enriched in the SML relative to the SSW, and temporal differences are a major driver of variability in surfactant concentrations, as demonstrated by the highest values recorded during a fall picoeukaryotic bloom. Surfactant concentrations showed a positive correlation with tryptophan-like FDOM, supporting a biogenic source of marine surfactants. Microbial community composition differed between the SML and SSW, with the SML enriched in small, resource-efficient taxa adapted to high-light and low-nutrient conditions. Significant correlations were observed between surfactant concentrations and diverse microbial taxa, including picoeukaryotic phytoplankton such as Ostreococcus, Bathycoccus, and Micromonas; heterotrophic bacteria such as the NS5 marine group, Pseudoalteromonas, SAR86, and Candidatus Actinomarina; as well as phagotrophic protists such as MAST-7B and Cercozoa, and parasitic dinoflagellates from the Dino-Group-I and Dino-Group-II clades. The diversity of surfactant associated microbial candidates suggests that surfactant production reflects a broader range of microbial processes than phytoplankton activity alone, with tryptophan-like FDOM capturing this integrated biological process more effectively than chlorophyll-a concentrations. These findings establish tryptophan-like FDOM as a promising proxy for predicting marine surfactant concentrations and highlight the need for an in-depth understanding of the diverse microbial sources of surfactants.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2026-3084', Anonymous Referee #1, 15 Jul 2026
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RC2: 'Comment on egusphere-2026-3084', Anonymous Referee #2, 16 Jul 2026
The manuscript by Agblemanyo et al. examines the possible biological sources of marine surfactants in the sea surface microlayer (SML) and subsurface water (SSW) at three different locations during summer 2022, and only one station during fall 2022, of the northwestern Atlantic. The authors combine measurements of dissolved organic matter (DOM), including fluorescent dissolved organic matter (FDOM), dissolved organic carbon (DOC), and surfactant concentration, with 16S/18S rRNA gene amplicon profiles. Their main findings are that DOC-normalized surfactant concentrations and tryptophan-like fluorescence were elevated in the SML, were highest during the fall Delaware Coast sampling, and were positively correlated. The authors further report differences in bacterial and protist community composition between SML and SSW and identify numerous taxa whose relative abundance correlates with surfactant concentrations and tryptophan-like fluorescence. On this basis, they propose tryptophan-like FDOM as a proxy for marine surfactants and identify candidate microbial producers or indicators.
The manuscript addresses an important and insufficiently constrained component of air-sea exchange: the biological origin and variability of surface-active organic matter at the ocean interface. The combined chemical, optical, and microbial measurements are potentially valuable, and the SML/SSW comparison is relevant to several fields. However, I don’t think that the current statistical analysis and interpretation support several of the strongest conclusions. Also, the manuscript sometimes reads (especially in the results section) like a random selection of differences and not a comprehensive description of the results. My biggest concerns are that season is confounded with station because fall sampling occurred at only one site, and that the authors discuss 'candidate surfactant producers' or 'microbial sources' based on correlation analyses alone. The taxonomic correlations are repeatedly interpreted as evidence for surfactant production. While the data demonstrate co-occurrence, it does not prove production. Also, ASV-environment correlations are declared significant, but the authors do not mention any multiple-testing control. I think that these issues affect the central claim of the manuscript; I therefore recommend a major revision.
-The manuscript repeatedly states that temporal differences are a major driver of surfactant variability and interprets the fall Delaware Coast observations as a seasonal or bloom effect. Yet the fall cruise sampled only the Delaware Coast station, whereas the summer cruise sampled three stations. Thus, “season” is confounded with cruise, sampling date, hydrographic conditions, and the Delaware Coast station revisited. The dataset cannot distinguish a general seasonal effect from a Delaware-specific event or from cruise-specific conditions. Therefore, the statement “temporal differences are a major driver of variability” is not justified. The authors should reframe this comparison as a limited repeat observation at one station and avoid generalizing beyond the sampled event. With this data, the authors cannot claim seasonal patterns.
- For the ASV-environment correlations, the network analysis identifies significant correlations between each ASV and the measured DOM variables using a significance threshold of p < 0.05. However, because hundreds of bacterial and protist ASVs were tested against multiple DOM variables, a very large number of statistical tests were performed. When so many tests are conducted, some correlations are expected to appear significant purely by chance. The manuscript does not indicate whether a multiple-testing correction (e.g., Benjamini–Hochberg false discovery rate) was applied to reduce this risk. Without such a correction, it is difficult to assess how many of the reported significant associations are truly robust. The authors should clarify whether multiple-testing correction was used, and if not, consider applying one. It would also be helpful to report the total number of tests performed and the number of significant associations remaining after correction.
- Many of the taxa identified as being associated with surfactants and tryptophan-like C1 were also most abundant in the Delaware Coast Fall samples, where both surfactant concentrations and tryptophan-like C1 reached their highest values. As a result, some of the observed correlations may reflect the unique environmental conditions of this sampling period rather than a direct relationship between individual taxa and surfactants. In other words, taxa that characterize the Delaware Fall community are likely to correlate with both variables simply because they co-occur under the same conditions. Therefore, it is difficult to disentangle the effects of DOM composition from those of “season”, station, or bloom state using pairwise correlations alone. The authors should acknowledge this, and the identified taxa should be presented as candidate taxa associated with surfactant-rich conditions rather than as biomarkers or potential surfactant producers. Furthermore, 16S/18S amplicons identify taxonomic markers, not expressed functions, metabolic rates, or causal interactions, so the authors need to be careful in inferring surfactant production.
- The authors claim a fall picoeukaryotic bloom based mainly on elevated chlorophyll-a, and the elevated chlorophyll at one event is not sufficient. They even acknowledge in line 240 that it is a “potential” bloom. If the authors want to claim it is a bloom, the authors could do a regional remote-sensing analysis using MODIS data to contextualize their single measurement.
- I’m not sure that using DOC concentrations to normalize the FDOM and surfactant concentrations is correct. Because both surfactant concentrations and FDOM components are expressed relative to DOC, the shared denominator could artificially strengthen their relationship. Do the authors also see correlations without normalizing the data?
- The authors rely on a sampling method that has yet to be published, so either that paper is published or the authors need to add substantially more detail and controls on the SML sampling. How do they know the rosette did not contaminate the microlayer? Are they artificially enriching a specific taxon?
-For sequencing, the authors did not report extraction blanks, PCR negatives, sequencing controls, etc. -The authors did not perform any analysis with environmental variables, why? This should be included.
- It is also not clear from Figure 2 that the microbial communities varied between the SML and SSW. There is clustering of the different stations, but there is no clear difference between the SML and SSW.
-There was no discussion about daytime and nighttime differences. Can the authors add some analysis and discussion?
-Figure 1. Don’t just put the box plots; add all the samples.
-Line318, shouldn’t it be 28?
Citation: https://doi.org/10.5194/egusphere-2026-3084-RC2
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- 1
Agblemanyo and colleagues report co-occurrent measurements of surfactant concentrations, fluorescent dissolved organic matter, and amplicon sequencing for bacteria and protists in the microlayer and subsurface waters from three regions and two seasons. The authors' results indicate that significant differences in surfactant concentrations exist between SML and SSW, seasons and regions. The authors show that surfactant concentrations are positively correlated with tryptophan-like FDOM, supporting a biogenic source of marine surfactants. Therefore, the authors suggest that tryptophan-like FDOM can be a predictor of surfactant concentrations. The datasets generated for this study are of high value and represent an important contribution to better understanding the role of surfactants, their biogenesis, and distribution in the water column. Analyses fulfil high standards of methodological rigour, figures are of great quality and carefully crafted, and conclusions and discussion follow a logical narrative. Despite this, I believe some minor concerns should be addressed to strengthen the conclusions presented and provide a more panoramic view of a complex microbial system. Please find them below.
1) One of the major claims presented in the study (Line 30, second result presented in the abstract): "Surfactant concentrations showed a positive correlation with tryptophan-like FDOM, supporting a biogenic source of marine surfactants" seems to have already been established previously. So, I suggest placing it as a confirming result rather than a main new result derived from this study. I suggest removing it from the abstract to better focus on the strengths of the Microlayer-SSW comparison.
2) Could subsection 3.4 be joined to the previous one (3.3)? This might help to improve the narrative and flow of the document.
3) Line 300-302. Comparing number of ASVs does not suggest higher or lower diversity if sampling sequencing effort or coverage is not taken into consideration. Furthermore, how conserved each segment of the different genes amplified influences the different level of resolution these might have; some of them can reach genus, others family. So, you are comparing apples with oranges, I don't think you can directly do this comparison, please check your assumptions.
4) Lines 302-308 can be collapsed by only presenting the results. It does read repetitive to me, but feel free to disregard.
5) Line 310: Please avoid using "/"; use "and," "or," "neither," etc. Be clear and don't let the reader interpret it.
6) Lines 324 to 337: All these statements should be supported either by showing the percentages in the numbers or, better, by conducting proper statistical tests. Otherwise, it is a subjective description of the figure.
7) Tables 3 and 4 and their description in the results. Please specify how these tests were done. I am assuming SSW and SML were collapsed somehow. But it might be that only one group was taken into consideration. When multiple variables are being used in the study, please be as specific as you can.
8) Lines 428 to 432: It is not as clear how surfactant and FDOM concentrations represent DOM composition. This might need a more detailed description, not only the statement between parentheses.
9) Figures 4 and 5: It would be interesting to analyse how well these clusters overlap with the SSW and SML enriched categorisation of the ASVs.
10) Before the discussion, I believe the results section would have benefitted from an analysis of interactions with physical variables (e.g., temperature, salinity, PAR, etc.) to strengthen the interpretation of the reported correlations (amplicons vs fDOM and surfactants). The only additional variable explored was chla concentration, and it was with a very specific objective. One could argue that it remains unclear whether the observed relationships (e.g., surfactant–tryptophan-like FDOM) are independent signals or whether they reflect shared covariation with another underlying driver. I recommend the authors include a covariation or interaction analysis (e.g., partial correlations, multivariate regression, or explicit testing against physical parameters) to better support the interpretation of these correlations.
11) Lines 550–551: This statement ("more aromatic and humified DOM is present [in the SSW] compared to the SML") lacks a supporting reference or link to the manuscript's own results (e.g., a specific figure or table). It reads counterintuitive to me. I thought aromatic and humified DOM accumulate in the SML relative to the SSW. I also suggest being more nuanced in the discussion, as the results only reflect a few specific spaces and times of sampling. For instance, the authors may have captured a specific season, bloom stage, or set of physicochemical conditions under which this pattern holds, and this context should be made explicit instead of being presented as a general statement.
I would also encourage the authors to frame this discussion in terms of DOM recalcitrance and the metabolic strategies of the bacterial lineages involved, rather than only cell-buoyancy/light-harvesting traits. For example, taxa such as SAR86 are specialized in degrading aromatic and structurally complex compounds in oligotrophic waters, and disentangling substrate preference from photoheterotrophic capacity (light-harvesting adaptations) would help clarify why particular lineages associate with the SML versus the SSW.
Finally, please be careful when binning taxonomically diverse genera (e.g., Caulobacter, Cupriavidus, Alteromonas, Comamonadaceae, Mesoflavibacter) into a single functional category ("heterotrophic lifestyles lacking light-harvesting adaptations"). These taxa differ substantially in ecology and genomic capacity, and the generalization should be softened or better justified based on each group's role in the different DOM degradation.