the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 12 Jun 2026
Stoichiometric deviation and regulatory mechanisms of AOU-nutrient ratio in the oligotrophic Northwest Pacific Ocean
Abstract. In oligotrophic oceans, the stoichiometric ratios of apparent oxygen utilization (AOU) to nutrients often deviate from the classical Redfield ratio, yet the mechanisms driving these deviations remain poorly constrained. Contrary to the commonly held view that ratios of AOU to nutrients are typically elevated, our study found that the mean ratios of AOU to dissolved inorganic nitrogen (DIN) and AOU to dissolved inorganic phosphorus (DIP) in the upper 2000 m of the oligotrophic Northwest Pacific are substantially lower than the classical Redfield ratios (8.6 and 138, respectively), measuring only 6.28 and 86.79, respectively. Physical mixing alone cannot explain these low ratios, as the region is strongly stratified. This persistent vertical isolation drives chronic nutrient limitation in surface waters, promoting phytoplankton to produce carbon‑rich transparent exopolymer particles (TEPs) with high C:N ratios. Meanwhile, the microbial community, dominated by Pelagibacter and Alteromonas, exhibits functional partitioning. Pelagibacter efficiently recycles small organic molecules, while Alteromonas degrades complex polymers and actively releases phosphate. This selective processing enhances nutrient regeneration relative to carbon oxidation, depressing the AOU/nutrient ratios. These findings suggest that biogeochemical models should account for such biological feedbacks to improve predictions of ocean carbon export and nutrient cycling under future climate scenarios.
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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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RC1: 'Comment on egusphere-2026-2947', Anonymous Referee #1, 28 Jun 2026
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AC1: 'Reply on RC1', Weichao Wu, 19 Jul 2026
Thank you very much for your constructive review of our manuscript. We have considered and addressed each of your comments point by point and revised the manuscript accordingly. In particular, we clarified the definition, parameter dependence, and uncertainty of rPreNO3 and rPrePO4; distinguished the processes operating in the upper, intermediate, and deep waters; moderated and refined the interpretation of TEP; added comparisons with previously published observations; and clarified the analytical procedures for POC and TEP, including the laboratory-generated xanthan gum calibration curve. We also revised the relevant figures, supplementary materials, terminology, and discussion to improve the accuracy, consistency, and clarity of the manuscript.
A detailed point-by-point response and the supplementary materials are provided in the attached files. We sincerely appreciate the referee’s valuable comments and suggestions.
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RC3: 'Reply on AC1', Anonymous Referee #1, 29 Jul 2026
The authors have carefully considered my comments and have made substantial and generally appropriate revisions to the manuscript. In particular, the revised manuscript now distinguishes the mechanisms operating in the upper, intermediate, and deep waters, clarifies the diagnostic rather than independent evidential role of residual preformed nutrients, and provides additional methodological information and literature comparisons for TEP. These revisions have substantially improved the clarity and balance of the manuscript.
I consider the manuscript suitable for publication after the following minor revisions.
1 the fDOM and fPOM issure
fDOM fPOM are defined as the fractions of total oxygen consumption attributable to DOM and POM remineralization, respectively. Therefore, I think these two fractions should satisfy the mass-balance constraint: fDOM + fPOM =1.
If this is the case and I am right, then the current sensitivity analysis varies fDOM and fPOM independently among 0.4, 0.5, and 0.6, producing 27 parameter combinations. Some of these combinations assign less or more than 100% of the total oxygen consumption to DOM and POM together and are therefore not physically consistent.
I recommend recalculating rPreNO₃ and rPrePO₄ under the above constraint. The corresponding means, ranges, and standard deviations should be updated in the manuscript, supplementary material, figures, and public dataset as necessary. The authors should also confirm whether the principal vertical patterns and interpretations remain unchanged after this recalculation.
- Interpretation of TEP abundance
The authors have appropriately acknowledged that the absolute TEP concentrations observed in this study fall within the relatively low range reported for oceanic environments. The newly added TEP-C/POC comparison is useful because it shows that TEP-associated carbon represents a substantial fraction of the relatively small POC pool in the study region.
Nevertheless, Table S1 also shows that the TEP concentrations and TEP-C/POC ratios reported here are not among the highest values observed globally. In particular, comparable or higher TEP-C/POC ratios have been reported from some other sites (Table S1). Therefore, statements such as the TEP-C/POC ratio being “generally higher than those observed in most productive coastal, shelf, and surface open-ocean environments” should be moderated.
I personally think a more accurate interpretation would be that the absolute TEP concentration is not exceptionally high on a global scale, but that TEP constitutes a substantial component of the local POC pool under the oligotrophic conditions of the study region. This relative importance makes TEP production a plausible contributor to the observed upper-ocean AOU/nutrient deviations, although it does not necessarily demonstrate that TEP is the sole or dominant driver. Eventually, further study is needed to reveal or confirm this point---particularly to check whether similar abnormal AOU/nutrient ratios are presence in those regions with similarly high TEP/POC ratios. This call for further study should also be included in the manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2947-RC3 -
AC2: 'Reply on RC3', Weichao Wu, 05 Aug 2026
We sincerely thank the reviewer for the constructive comments on our manuscript, and we greatly appreciate the reviewer’s recognition of the improvements made in the revised version.
We have carefully addressed both remaining concerns raised by the reviewer. For the first issue, we recalculated rPreNO3 and rPrePO4 using nine mass-balance-constrained parameter combinations and confirmed that all principal vertical patterns and interpretations remain unchanged. For the second issue, we have moderated the overstatement regarding TEP-C/POC ratios in the Results section and refined the Discussion to acknowledge TEP as a plausible but not exclusive contributor, while also incorporating the recommended call for future studies. All corresponding changes have been made to the manuscript, Supplementary Materials, figures, and the public dataset. The detailed point-by-point responses and other materials are provided in the attached files.
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RC3: 'Reply on AC1', Anonymous Referee #1, 29 Jul 2026
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AC1: 'Reply on RC1', Weichao Wu, 19 Jul 2026
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RC2: 'Comment on egusphere-2026-2947', Anonymous Referee #2, 27 Jul 2026
The manuscript by Tian et al. studies the low AOU to nutrient (DIN and DIP) ratios in the oligotrophic tropical Northwest Pacific by combining hydrographic, biogeochemical and microbial community analysis. They found consistently low AOU/DIN and AOU/DIP ratios compared to Redfield ratios, together with high TEP concentrations in the upper water column and depth-depended shifts. The results indicate that variations in TEP abundance and the functional composition of microbial communities are closely associated with nutrient regeneration in their working area. Therefore, the manuscript is of interest as it improves the understanding of how microbial processes and organic matter regulate nutrient regeneration and carbon cycling in the ocean.
The dataset is of high quality, and the main findings are robust and supported by the analyses presented. However, major revisions are necessary to better explain certain methodological aspects and to improve the organization and terminology of the results section.
General remarks:
- The calculation of residual preNO3 and prePO4 relies on fixed DOM/POM remineralization stoichiometries adopted from previous studies, while the main conclusion of the manuscript is that Redfield-type stoichiometric relationships break down in the study region. The authors should discuss the consistency of applying fixed remineralization ratios under these conditions and clarify the uncertainty associated with this assumption.
- Throughout the manuscript, I was occasionally confused about the level at which the reported ratios are calculated and discussed. In some sections, the text refers to ratios for specific water masses, whereas in others it refers to the three predefined depth intervals (0-300 m, 300-1000 m, and >1000 m). However, the terminology is not always used consistently, and at times the depth intervals appear to be discussed as if they were distinct water masses. This makes it difficult to distinguish whether a given result relates to a hydrographically defined water mass, a depth-based grouping, or the entire water column. I encourage the authors to carefully review the manuscript and use consistent terminology throughout. In particular, the distinction between water masses and depth intervals should be made explicit at all times. These represent fundamentally different ways of grouping the data, yet the distinction between them is not always clear in the current text, which can make the results difficult to interpret.
- More broadly, I am not fully convinced that the current presentation of the results is the most effective way to communicate the findings. Much of the Results section is structured around analyses of the individually identified water masses, yet the Discussion predominantly focuses on the three depth intervals. This raises the question of what additional insight is gained from the detailed water-mass-specific analyses if the subsequent interpretation is largely based on the depth-based grouping. The rationale and added value of the water-mass analysis therefore deserve further clarification. As an alternative, I would suggest retaining the T-S diagram to define and visualize the identified water masses, but reconsidering the presentation of Figures 2 and 3. Rather than organizing these results by individual water masses, depth-profile figures of the relevant parameters might provide a clearer overview of vertical gradients and stratification while remaining more closely aligned with the depth-interval framework that is ultimately emphasized in the Discussion. Such an approach could also help avoid some of the terminology issues arising from the current mixture of water-mass-based and depth-based analyses.
Specific remarks:
L131: Why were nutrients samples preserved with chloroform? Chloroform is generally not recommended as a preservation method for dissolved nutrient samples due to its volatility and potential impacts on nutrient concentrations, particularly phosphate, nitrate, nitrite, and ammonia, during storage. Previous studies have reported possible nutrient alterations associated with chloroform preservation, and alternative approaches such as filtration followed by freezing are more commonly applied in marine biogeochemical studies (see Kim et al., 2025 and references therein).
L160: How much time elapsed between sample collection and chlorophyll extraction?
L211/L223: Why were general stoichiometric ratios applied rather than the water mass-specific stoichiometric relationships identified in the study region? Since the manuscript itself demonstrates that the observed AOU-to-nutrient ratios deviate from the expected Redfield stoichiometry, it is unclear why a stoichiometric framework that does not adequately represent the investigated water masses is used for subsequent analyses. The authors should discuss how this choice may affect the calculated ratios, the interpretation of nutrient regeneration processes, and the overall conclusions of the study.
L212: Since NO3meas is defined as the sum of NO3-N and NO2-N concentrations, please refer to it as NOx.
L224-226: To what extent is this assumption valid if one of the main conclusions of the paper is that the Redfield ratio does not apply?
L369: In what depth is the mixed layer depth? Shouldn’t the uppermost part of the water column, which is mixed by wind and wave-driven turbulences, be excluded from the analysis?
L368: Why was this analysis not also performed separately for the individual water masses? Earlier in the manuscript, the analyses are conducted on a water-mass-specific basis, whereas here results are presented as a bulk signal across multiple depth layers. What is the rationale for changing the approach at this stage?
L371: Is this really a single water mass? Figure 5 suggests that the upper 300 m contains more than one water mass. Please be careful with the terminology and ensure that the distinction between water masses and depth intervals is made consistently throughout the manuscript.
L430: What about denitrification in anoxic microsites close to particles (e.g., Bianchi et al., 2018; Wan et al., 2023)?
Figure 3: I’m missing some very basic depth profiles plots of key water mass properties (also temperature, salinity, AOU, DIN, P, TEP, …). Such figures would help readers better visualize the stratification and support the separation of the water column into the three depth intervals (0-300 m, 300-1000 m, and >1000 m
References
Bianchi, D., Weber, T. S., Kiko, R., and Deutsch, C.: Global niche of marine anaerobic metabolisms expanded by particle microenvironments, Nat. Geosci., 11, 263–268, https://doi.org/10.1038/s41561-018-0081-0, 2018.
Kim, M. S., Choi, M. S., and Rhee, T. S.: Comparative assessment of preservation methods for major nutrients in polar seawater, Mar. Chem., 272, 104546, https://doi.org/10.1016/j.marchem.2025.104546, 2025.
Wan, X. S., Sheng, H.-X., Liu, L., Shen, H., Tang, W., Zou, W., Xu, M. N., Zheng, Z., Tan, E., Chen, M., Zhang, Y., Ward, B. B., and Kao, S.-J.: Particle-associated denitrification is the primary source of N2O in oxic coastal waters, Nat. Commun., 14, 8280, https://doi.org/10.1038/s41467-023-43997-3, 2023.
Citation: https://doi.org/10.5194/egusphere-2026-2947-RC2 -
AC4: 'Reply on RC2', Weichao Wu, 19 Aug 2026
Dear Referee,
We sincerely thank you for your careful assessment and constructive comments. In response, we have substantially revised the manuscript to improve its methodological transparency, analytical consistency, and presentation. The principal revisions are summarized below.
1. We clarified that rPreNOx and rPrePO4 are parameter dependent diagnostic residuals derived from published reference stoichiometries, rather than estimates of true preformed nutrients or independent evidence of stoichiometric deviation. Nine mass balance constrained parameter combinations were evaluated to assess parameter sensitivity, while our main conclusions remain based on regressions using directly measured AOU and nutrient concentrations.
2. We reorganized the manuscript around three hydrographic groups: upper, intermediate, and deep waters. The eight named water masses are now retained only to establish the hydrographic context. In addition, sensitivity analyses confirmed that neither the alternative fixed depth grouping nor the exclusion of mixed layer observations significantly changed the regression slopes.
3. Figures 2–5 and 7, together with the corresponding Results and Discussion, were reorganized to present vertical profiles and consistent comparisons among the three hydrographic groups.
4. We expanded the methodological information concerning nutrient and chlorophyll-a sample preservation and standardized the use of NOx throughout the manuscript.
5. We refined the mechanistic interpretation of TEP by acknowledging its modest absolute concentration while emphasizing the substantial estimated TEP-C contribution to POC. TEP is now presented as one plausible contributor rather than a principal driver. We also explicitly discuss the possibility and uncertainty of denitrification within particle microsites.
Detailed point-by-point responses, sensitivity analyses, revised figures and tables, and the corresponding text changes are provided in the attached response document.
We thank the referee again for the valuable comments, which have helped us substantially improve the clarity and rigor of the manuscript.
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RC4: 'Comment on egusphere-2026-2947', Anonymous Referee #1, 06 Aug 2026
I think the authors have replied all my comments and I have no further questions on this manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2947-RC4 -
AC3: 'Reply on RC4', Weichao Wu, 11 Aug 2026
Dear Referee,
Thank you for your careful review and for confirming that your comments have been satisfactorily addressed. We sincerely appreciate your constructive suggestions, which have helped us improve the manuscript.
Sincerely,
The authorsCitation: https://doi.org/10.5194/egusphere-2026-2947-AC3
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AC3: 'Reply on RC4', Weichao Wu, 11 Aug 2026
Peer review completion
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2026-2947', Anonymous Referee #1, 28 Jun 2026
From the observed AOU/nutrient ratios, the deviations from the classical Redfield stoichiometry are actually relatively modest. Nevertheless, the authors provide a detailed mechanistic interpretation of these subtle deviations from multiple perspectives, particularly focusing on TEP production and microbial metabolic strategies. In my opinion, this represents an interesting and worthwhile attempt.
The central hypothesis proposed by the authors is that strong stratification in the TNWP leads to chronic nutrient limitation in surface waters, which promotes the production of carbon-rich TEP by phytoplankton. Subsequently, microbial communities selectively degrade nitrogen- and phosphorus-rich organic components while preferentially regenerating phosphorus, resulting in nutrient regeneration exceeding organic carbon oxidation and ultimately producing AOU/nutrient ratios slightly lower than the classical Redfield values.
From the apparent regression slopes, however, the AOU/nutrient ratios reported here are substantially higher than those previously reported by Zhu et al. in the northern South China Sea (e.g., AOU/DIN = 3.09 in Zhu et al. versus 6.28 in the present study). In my view, these represent two fundamentally different scenarios. The extremely low ratios observed by Zhu et al. were likely dominated by physical processes such as water-mass mixing, whereas the present study represents a typical open-ocean environment where biogeochemical processes are expected to play a much more important role.
TEP itself is a carbon-rich, nitrogen- and phosphorus-poor organic material. From the perspective of remineralization, degradation of TEP consumes oxygen but releases relatively little nitrogen and phosphorus. Consequently, TEP degradation would be expected to increase, rather than decrease, the AOU/nutrient ratios relative to the Redfield expectation. Therefore, the degradation of TEP alone does not appear to support the mechanism proposed in this manuscript.
In contrast, from the perspective of TEP production, the mechanism is much more convincing. TEP production originates from phytoplankton photosynthesis, during which oxygen is produced and carbon is fixed, whereas the associated consumption of nitrogen and phosphorus is substantially lower than predicted by the Redfield ratio because of the high C:N composition of TEP. Under this scenario, AOU decreases whereas nutrient concentrations decrease much less than expected, potentially leading to relatively low AOU/nutrient ratios. Therefore, it seems reasonable that phytoplankton production of TEP could contribute to reduced AOU/nutrient ratios within the euphotic zone, or approximately the upper 0–300 m where active photosynthesis occurs.
Overall, I consider the attempt to explain the reduced AOU/nutrient ratios in the upper ocean from the perspective of TEP production to be novel and potentially important. My major comments and concerns are as follows:
Major:
1. Use and interpretation of preformed nutrients
The use of preformed nitrate (PreNO₃) and preformed phosphate (PrePO₄) requires additional caution. The classical concept of preformed nutrients is based on the assumption that organic matter remineralization and nutrient regeneration follow a prescribed stoichiometric relationship, typically the Redfield ratio (or a fixed empirical remineralization stoichiometry). However, the central premise of the present manuscript is precisely that organic matter remineralization in the study region deviates from the classical Redfield stoichiometry. This creates a potential inconsistency between the methodological assumptions and the scientific conclusions.
For this reason, I do not suggest removing the calculations of PreNO₃ and PrePO₄, as they may still serve as useful diagnostic residuals. However, I recommend avoiding interpreting them as the true "preformed nutrients." Instead, they should be presented as residual indicators derived under a predefined remineralization stoichiometry. Otherwise, there is a risk of circular reasoning: the manuscript uses preformed nutrients calculated under an assumed stoichiometric relationship to demonstrate that the remineralization stoichiometry itself deviates from that assumption. This logical issue should be explicitly acknowledged and discussed.
In addition, the manuscript adopts the modified approach proposed by Letscher and Villareal by introducing different remineralization coefficients for DOM and POM, which is intended to improve the realism of the calculations. This is good. Nevertheless, the parameters used in the calculations (fDOM, fPOM, rDOM, and rPOM) remain empirical assumptions rather than values constrained by observations from the study region. In particular, Table 1 lists multiple candidate values of rPOM, yet the manuscript does not explain which value was ultimately adopted or the criteria used for selecting among them. Consequently, the calculated PreNO₃ and PrePO₄ are highly dependent on these empirical parameterizations and therefore should not be regarded as independent evidence supporting the proposed mechanism responsible for the low AOU/nutrient ratios. Rather, they should be interpreted as model-dependent diagnostic quantities whose uncertainties deserve further discussion.
2. Distinguishing whole-water-column observations from layer-specific mechanisms
According to the authors' own results, statistically significant AOU–nutrient relationships are observed only in the upper (0–300 m) and intermediate (300–1000 m) water masses, whereas no significant relationships exist below 1000 m (p > 0.05). I therefore recommend that the authors more clearly distinguish between the statistical patterns derived from the entire water column and the mechanisms operating within individual water masses.
If the proposed TEP-driven mechanism is intended to explain the low AOU/nutrient ratios throughout the entire water column, additional evidence is needed to demonstrate that its influence extends from the surface into the mesopelagic and deeper waters. Conversely, if the mechanism is primarily intended to explain the upper ocean, the corresponding statements in the Abstract, Discussion, and Conclusions should be moderated accordingly. In particular, a mechanism fundamentally linked to surface phytoplankton production should not be directly extrapolated to the deep ocean, especially where no statistically significant AOU–nutrient relationships are observed.
Furthermore, it should be noted that the production of TEP and the degradation of TEP are two distinct biogeochemical processes that are expected to have different, and potentially opposite, effects on AOU/nutrient stoichiometry. Current understanding suggests that TEP is produced predominantly within the euphotic zone by phytoplankton, whereas TEP observed in mesopelagic waters mainly represents exported material undergoing degradation rather than in situ production. The manuscript would therefore benefit from explicitly distinguishing between surface TEP production and subsurface TEP remineralization when discussing the mechanisms responsible for the observed AOU/nutrient ratios. This distinction is particularly important because TEP production and TEP degradation may influence AOU/nutrient stoichiometry in different directions.
3. Strength of the evidence linking TEP to the observed AOU/nutrient ratios
Another issue concerns the interpretation of the TEP observations. Based on the reported concentrations, the TEP levels observed in this study are generally within the low to moderately low range compared with those reported from the global ocean. Even within the oligotrophic western tropical North Pacific, the measured concentrations appear to be lower than those reported in previous studies, and they are substantially lower than those typically observed in productive coastal regions, frontal systems, or the surface Southern Ocean. Therefore, the statement that TEP-related process is responsible for the observed low AOU/nutrient ratios should be made with greater caution.
In other words, the manuscript currently assumes that TEP abundance is the principal driver of the stoichiometric deviation, yet the observational evidence demonstrates only the presence of TEP rather than an exceptional accumulation relative to other oceanic regions. Therefore, the authors should better justify why relatively modest TEP concentrations are sufficient to produce measurable deviations in AOU/nutrient stoichiometry. Alternatively, the discussion could place greater emphasis on the quality, composition, or turnover of TEP, rather than its absolute concentration, as these characteristics may be more directly linked to remineralization stoichiometry than concentration alone.
Minor or specific:
The reported analytical precision of the POC measurements deserves further clarification. In general, the instrumental precision of an elemental analyzer for carbon determination is typically on the order of approximately 1% under routine laboratory conditions. For real samples, however, the overall analytical precision is usually lower because additional uncertainties are introduced during sample collection, filtration, acidification (or acid fumigation), drying, and other pretreatment procedures. Therefore, the reported analytical precision of 0.8‰ appears to be exceptionally high—nearly two orders of magnitude better than the analytical precision commonly achieved in routine laboratory measurements of marine suspended particulate organic carbon. I am therefore curious about how this level of precision was achieved. Does this value refer to the repeatability of the elemental analyzer itself, the precision of repeated analyses of laboratory standards, or the overall analytical precision including sample pretreatment? Alternatively, could this simply be a typographical error? I recommend that the authors clarify how this value was determined and what it specifically represents.
The description of the TEP analytical method requires clarification. The current protocol omits several key steps of the standard Alcian Blue assay (e.g., staining and washing), making it unclear whether the standard method was actually followed or whether these procedures were inadvertently omitted from the manuscript. In addition, the authors should clarify whether the xanthan gum calibration curve was established under their own experimental conditions or directly adopted from Bittar et al. (2018), as calibration curves are generally expected to be generated within each laboratory to ensure quantitative reliability.
What do the red arrows mean in fig 2a?
Citation: https://doi.org/10.5194/egusphere-2026-2947-RC1 -
AC1: 'Reply on RC1', Weichao Wu, 19 Jul 2026
Thank you very much for your constructive review of our manuscript. We have considered and addressed each of your comments point by point and revised the manuscript accordingly. In particular, we clarified the definition, parameter dependence, and uncertainty of rPreNO3 and rPrePO4; distinguished the processes operating in the upper, intermediate, and deep waters; moderated and refined the interpretation of TEP; added comparisons with previously published observations; and clarified the analytical procedures for POC and TEP, including the laboratory-generated xanthan gum calibration curve. We also revised the relevant figures, supplementary materials, terminology, and discussion to improve the accuracy, consistency, and clarity of the manuscript.
A detailed point-by-point response and the supplementary materials are provided in the attached files. We sincerely appreciate the referee’s valuable comments and suggestions.
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RC3: 'Reply on AC1', Anonymous Referee #1, 29 Jul 2026
The authors have carefully considered my comments and have made substantial and generally appropriate revisions to the manuscript. In particular, the revised manuscript now distinguishes the mechanisms operating in the upper, intermediate, and deep waters, clarifies the diagnostic rather than independent evidential role of residual preformed nutrients, and provides additional methodological information and literature comparisons for TEP. These revisions have substantially improved the clarity and balance of the manuscript.
I consider the manuscript suitable for publication after the following minor revisions.
1 the fDOM and fPOM issure
fDOM fPOM are defined as the fractions of total oxygen consumption attributable to DOM and POM remineralization, respectively. Therefore, I think these two fractions should satisfy the mass-balance constraint: fDOM + fPOM =1.
If this is the case and I am right, then the current sensitivity analysis varies fDOM and fPOM independently among 0.4, 0.5, and 0.6, producing 27 parameter combinations. Some of these combinations assign less or more than 100% of the total oxygen consumption to DOM and POM together and are therefore not physically consistent.
I recommend recalculating rPreNO₃ and rPrePO₄ under the above constraint. The corresponding means, ranges, and standard deviations should be updated in the manuscript, supplementary material, figures, and public dataset as necessary. The authors should also confirm whether the principal vertical patterns and interpretations remain unchanged after this recalculation.
- Interpretation of TEP abundance
The authors have appropriately acknowledged that the absolute TEP concentrations observed in this study fall within the relatively low range reported for oceanic environments. The newly added TEP-C/POC comparison is useful because it shows that TEP-associated carbon represents a substantial fraction of the relatively small POC pool in the study region.
Nevertheless, Table S1 also shows that the TEP concentrations and TEP-C/POC ratios reported here are not among the highest values observed globally. In particular, comparable or higher TEP-C/POC ratios have been reported from some other sites (Table S1). Therefore, statements such as the TEP-C/POC ratio being “generally higher than those observed in most productive coastal, shelf, and surface open-ocean environments” should be moderated.
I personally think a more accurate interpretation would be that the absolute TEP concentration is not exceptionally high on a global scale, but that TEP constitutes a substantial component of the local POC pool under the oligotrophic conditions of the study region. This relative importance makes TEP production a plausible contributor to the observed upper-ocean AOU/nutrient deviations, although it does not necessarily demonstrate that TEP is the sole or dominant driver. Eventually, further study is needed to reveal or confirm this point---particularly to check whether similar abnormal AOU/nutrient ratios are presence in those regions with similarly high TEP/POC ratios. This call for further study should also be included in the manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2947-RC3 -
AC2: 'Reply on RC3', Weichao Wu, 05 Aug 2026
We sincerely thank the reviewer for the constructive comments on our manuscript, and we greatly appreciate the reviewer’s recognition of the improvements made in the revised version.
We have carefully addressed both remaining concerns raised by the reviewer. For the first issue, we recalculated rPreNO3 and rPrePO4 using nine mass-balance-constrained parameter combinations and confirmed that all principal vertical patterns and interpretations remain unchanged. For the second issue, we have moderated the overstatement regarding TEP-C/POC ratios in the Results section and refined the Discussion to acknowledge TEP as a plausible but not exclusive contributor, while also incorporating the recommended call for future studies. All corresponding changes have been made to the manuscript, Supplementary Materials, figures, and the public dataset. The detailed point-by-point responses and other materials are provided in the attached files.
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RC3: 'Reply on AC1', Anonymous Referee #1, 29 Jul 2026
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AC1: 'Reply on RC1', Weichao Wu, 19 Jul 2026
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RC2: 'Comment on egusphere-2026-2947', Anonymous Referee #2, 27 Jul 2026
The manuscript by Tian et al. studies the low AOU to nutrient (DIN and DIP) ratios in the oligotrophic tropical Northwest Pacific by combining hydrographic, biogeochemical and microbial community analysis. They found consistently low AOU/DIN and AOU/DIP ratios compared to Redfield ratios, together with high TEP concentrations in the upper water column and depth-depended shifts. The results indicate that variations in TEP abundance and the functional composition of microbial communities are closely associated with nutrient regeneration in their working area. Therefore, the manuscript is of interest as it improves the understanding of how microbial processes and organic matter regulate nutrient regeneration and carbon cycling in the ocean.
The dataset is of high quality, and the main findings are robust and supported by the analyses presented. However, major revisions are necessary to better explain certain methodological aspects and to improve the organization and terminology of the results section.
General remarks:
- The calculation of residual preNO3 and prePO4 relies on fixed DOM/POM remineralization stoichiometries adopted from previous studies, while the main conclusion of the manuscript is that Redfield-type stoichiometric relationships break down in the study region. The authors should discuss the consistency of applying fixed remineralization ratios under these conditions and clarify the uncertainty associated with this assumption.
- Throughout the manuscript, I was occasionally confused about the level at which the reported ratios are calculated and discussed. In some sections, the text refers to ratios for specific water masses, whereas in others it refers to the three predefined depth intervals (0-300 m, 300-1000 m, and >1000 m). However, the terminology is not always used consistently, and at times the depth intervals appear to be discussed as if they were distinct water masses. This makes it difficult to distinguish whether a given result relates to a hydrographically defined water mass, a depth-based grouping, or the entire water column. I encourage the authors to carefully review the manuscript and use consistent terminology throughout. In particular, the distinction between water masses and depth intervals should be made explicit at all times. These represent fundamentally different ways of grouping the data, yet the distinction between them is not always clear in the current text, which can make the results difficult to interpret.
- More broadly, I am not fully convinced that the current presentation of the results is the most effective way to communicate the findings. Much of the Results section is structured around analyses of the individually identified water masses, yet the Discussion predominantly focuses on the three depth intervals. This raises the question of what additional insight is gained from the detailed water-mass-specific analyses if the subsequent interpretation is largely based on the depth-based grouping. The rationale and added value of the water-mass analysis therefore deserve further clarification. As an alternative, I would suggest retaining the T-S diagram to define and visualize the identified water masses, but reconsidering the presentation of Figures 2 and 3. Rather than organizing these results by individual water masses, depth-profile figures of the relevant parameters might provide a clearer overview of vertical gradients and stratification while remaining more closely aligned with the depth-interval framework that is ultimately emphasized in the Discussion. Such an approach could also help avoid some of the terminology issues arising from the current mixture of water-mass-based and depth-based analyses.
Specific remarks:
L131: Why were nutrients samples preserved with chloroform? Chloroform is generally not recommended as a preservation method for dissolved nutrient samples due to its volatility and potential impacts on nutrient concentrations, particularly phosphate, nitrate, nitrite, and ammonia, during storage. Previous studies have reported possible nutrient alterations associated with chloroform preservation, and alternative approaches such as filtration followed by freezing are more commonly applied in marine biogeochemical studies (see Kim et al., 2025 and references therein).
L160: How much time elapsed between sample collection and chlorophyll extraction?
L211/L223: Why were general stoichiometric ratios applied rather than the water mass-specific stoichiometric relationships identified in the study region? Since the manuscript itself demonstrates that the observed AOU-to-nutrient ratios deviate from the expected Redfield stoichiometry, it is unclear why a stoichiometric framework that does not adequately represent the investigated water masses is used for subsequent analyses. The authors should discuss how this choice may affect the calculated ratios, the interpretation of nutrient regeneration processes, and the overall conclusions of the study.
L212: Since NO3meas is defined as the sum of NO3-N and NO2-N concentrations, please refer to it as NOx.
L224-226: To what extent is this assumption valid if one of the main conclusions of the paper is that the Redfield ratio does not apply?
L369: In what depth is the mixed layer depth? Shouldn’t the uppermost part of the water column, which is mixed by wind and wave-driven turbulences, be excluded from the analysis?
L368: Why was this analysis not also performed separately for the individual water masses? Earlier in the manuscript, the analyses are conducted on a water-mass-specific basis, whereas here results are presented as a bulk signal across multiple depth layers. What is the rationale for changing the approach at this stage?
L371: Is this really a single water mass? Figure 5 suggests that the upper 300 m contains more than one water mass. Please be careful with the terminology and ensure that the distinction between water masses and depth intervals is made consistently throughout the manuscript.
L430: What about denitrification in anoxic microsites close to particles (e.g., Bianchi et al., 2018; Wan et al., 2023)?
Figure 3: I’m missing some very basic depth profiles plots of key water mass properties (also temperature, salinity, AOU, DIN, P, TEP, …). Such figures would help readers better visualize the stratification and support the separation of the water column into the three depth intervals (0-300 m, 300-1000 m, and >1000 m
References
Bianchi, D., Weber, T. S., Kiko, R., and Deutsch, C.: Global niche of marine anaerobic metabolisms expanded by particle microenvironments, Nat. Geosci., 11, 263–268, https://doi.org/10.1038/s41561-018-0081-0, 2018.
Kim, M. S., Choi, M. S., and Rhee, T. S.: Comparative assessment of preservation methods for major nutrients in polar seawater, Mar. Chem., 272, 104546, https://doi.org/10.1016/j.marchem.2025.104546, 2025.
Wan, X. S., Sheng, H.-X., Liu, L., Shen, H., Tang, W., Zou, W., Xu, M. N., Zheng, Z., Tan, E., Chen, M., Zhang, Y., Ward, B. B., and Kao, S.-J.: Particle-associated denitrification is the primary source of N2O in oxic coastal waters, Nat. Commun., 14, 8280, https://doi.org/10.1038/s41467-023-43997-3, 2023.
Citation: https://doi.org/10.5194/egusphere-2026-2947-RC2 -
AC4: 'Reply on RC2', Weichao Wu, 19 Aug 2026
Dear Referee,
We sincerely thank you for your careful assessment and constructive comments. In response, we have substantially revised the manuscript to improve its methodological transparency, analytical consistency, and presentation. The principal revisions are summarized below.
1. We clarified that rPreNOx and rPrePO4 are parameter dependent diagnostic residuals derived from published reference stoichiometries, rather than estimates of true preformed nutrients or independent evidence of stoichiometric deviation. Nine mass balance constrained parameter combinations were evaluated to assess parameter sensitivity, while our main conclusions remain based on regressions using directly measured AOU and nutrient concentrations.
2. We reorganized the manuscript around three hydrographic groups: upper, intermediate, and deep waters. The eight named water masses are now retained only to establish the hydrographic context. In addition, sensitivity analyses confirmed that neither the alternative fixed depth grouping nor the exclusion of mixed layer observations significantly changed the regression slopes.
3. Figures 2–5 and 7, together with the corresponding Results and Discussion, were reorganized to present vertical profiles and consistent comparisons among the three hydrographic groups.
4. We expanded the methodological information concerning nutrient and chlorophyll-a sample preservation and standardized the use of NOx throughout the manuscript.
5. We refined the mechanistic interpretation of TEP by acknowledging its modest absolute concentration while emphasizing the substantial estimated TEP-C contribution to POC. TEP is now presented as one plausible contributor rather than a principal driver. We also explicitly discuss the possibility and uncertainty of denitrification within particle microsites.
Detailed point-by-point responses, sensitivity analyses, revised figures and tables, and the corresponding text changes are provided in the attached response document.
We thank the referee again for the valuable comments, which have helped us substantially improve the clarity and rigor of the manuscript.
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RC4: 'Comment on egusphere-2026-2947', Anonymous Referee #1, 06 Aug 2026
I think the authors have replied all my comments and I have no further questions on this manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2947-RC4 -
AC3: 'Reply on RC4', Weichao Wu, 11 Aug 2026
Dear Referee,
Thank you for your careful review and for confirming that your comments have been satisfactorily addressed. We sincerely appreciate your constructive suggestions, which have helped us improve the manuscript.
Sincerely,
The authorsCitation: https://doi.org/10.5194/egusphere-2026-2947-AC3
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AC3: 'Reply on RC4', Weichao Wu, 11 Aug 2026
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Detong Tian
Jinming Song
Yunping Xu
Feng Zhao
Jun Ma
Shanshan Liu
Muhammad Inayat Ullah Khan
Weichao Wu
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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From the observed AOU/nutrient ratios, the deviations from the classical Redfield stoichiometry are actually relatively modest. Nevertheless, the authors provide a detailed mechanistic interpretation of these subtle deviations from multiple perspectives, particularly focusing on TEP production and microbial metabolic strategies. In my opinion, this represents an interesting and worthwhile attempt.
The central hypothesis proposed by the authors is that strong stratification in the TNWP leads to chronic nutrient limitation in surface waters, which promotes the production of carbon-rich TEP by phytoplankton. Subsequently, microbial communities selectively degrade nitrogen- and phosphorus-rich organic components while preferentially regenerating phosphorus, resulting in nutrient regeneration exceeding organic carbon oxidation and ultimately producing AOU/nutrient ratios slightly lower than the classical Redfield values.
From the apparent regression slopes, however, the AOU/nutrient ratios reported here are substantially higher than those previously reported by Zhu et al. in the northern South China Sea (e.g., AOU/DIN = 3.09 in Zhu et al. versus 6.28 in the present study). In my view, these represent two fundamentally different scenarios. The extremely low ratios observed by Zhu et al. were likely dominated by physical processes such as water-mass mixing, whereas the present study represents a typical open-ocean environment where biogeochemical processes are expected to play a much more important role.
TEP itself is a carbon-rich, nitrogen- and phosphorus-poor organic material. From the perspective of remineralization, degradation of TEP consumes oxygen but releases relatively little nitrogen and phosphorus. Consequently, TEP degradation would be expected to increase, rather than decrease, the AOU/nutrient ratios relative to the Redfield expectation. Therefore, the degradation of TEP alone does not appear to support the mechanism proposed in this manuscript.
In contrast, from the perspective of TEP production, the mechanism is much more convincing. TEP production originates from phytoplankton photosynthesis, during which oxygen is produced and carbon is fixed, whereas the associated consumption of nitrogen and phosphorus is substantially lower than predicted by the Redfield ratio because of the high C:N composition of TEP. Under this scenario, AOU decreases whereas nutrient concentrations decrease much less than expected, potentially leading to relatively low AOU/nutrient ratios. Therefore, it seems reasonable that phytoplankton production of TEP could contribute to reduced AOU/nutrient ratios within the euphotic zone, or approximately the upper 0–300 m where active photosynthesis occurs.
Overall, I consider the attempt to explain the reduced AOU/nutrient ratios in the upper ocean from the perspective of TEP production to be novel and potentially important. My major comments and concerns are as follows:
Major:
1. Use and interpretation of preformed nutrients
The use of preformed nitrate (PreNO₃) and preformed phosphate (PrePO₄) requires additional caution. The classical concept of preformed nutrients is based on the assumption that organic matter remineralization and nutrient regeneration follow a prescribed stoichiometric relationship, typically the Redfield ratio (or a fixed empirical remineralization stoichiometry). However, the central premise of the present manuscript is precisely that organic matter remineralization in the study region deviates from the classical Redfield stoichiometry. This creates a potential inconsistency between the methodological assumptions and the scientific conclusions.
For this reason, I do not suggest removing the calculations of PreNO₃ and PrePO₄, as they may still serve as useful diagnostic residuals. However, I recommend avoiding interpreting them as the true "preformed nutrients." Instead, they should be presented as residual indicators derived under a predefined remineralization stoichiometry. Otherwise, there is a risk of circular reasoning: the manuscript uses preformed nutrients calculated under an assumed stoichiometric relationship to demonstrate that the remineralization stoichiometry itself deviates from that assumption. This logical issue should be explicitly acknowledged and discussed.
In addition, the manuscript adopts the modified approach proposed by Letscher and Villareal by introducing different remineralization coefficients for DOM and POM, which is intended to improve the realism of the calculations. This is good. Nevertheless, the parameters used in the calculations (fDOM, fPOM, rDOM, and rPOM) remain empirical assumptions rather than values constrained by observations from the study region. In particular, Table 1 lists multiple candidate values of rPOM, yet the manuscript does not explain which value was ultimately adopted or the criteria used for selecting among them. Consequently, the calculated PreNO₃ and PrePO₄ are highly dependent on these empirical parameterizations and therefore should not be regarded as independent evidence supporting the proposed mechanism responsible for the low AOU/nutrient ratios. Rather, they should be interpreted as model-dependent diagnostic quantities whose uncertainties deserve further discussion.
2. Distinguishing whole-water-column observations from layer-specific mechanisms
According to the authors' own results, statistically significant AOU–nutrient relationships are observed only in the upper (0–300 m) and intermediate (300–1000 m) water masses, whereas no significant relationships exist below 1000 m (p > 0.05). I therefore recommend that the authors more clearly distinguish between the statistical patterns derived from the entire water column and the mechanisms operating within individual water masses.
If the proposed TEP-driven mechanism is intended to explain the low AOU/nutrient ratios throughout the entire water column, additional evidence is needed to demonstrate that its influence extends from the surface into the mesopelagic and deeper waters. Conversely, if the mechanism is primarily intended to explain the upper ocean, the corresponding statements in the Abstract, Discussion, and Conclusions should be moderated accordingly. In particular, a mechanism fundamentally linked to surface phytoplankton production should not be directly extrapolated to the deep ocean, especially where no statistically significant AOU–nutrient relationships are observed.
Furthermore, it should be noted that the production of TEP and the degradation of TEP are two distinct biogeochemical processes that are expected to have different, and potentially opposite, effects on AOU/nutrient stoichiometry. Current understanding suggests that TEP is produced predominantly within the euphotic zone by phytoplankton, whereas TEP observed in mesopelagic waters mainly represents exported material undergoing degradation rather than in situ production. The manuscript would therefore benefit from explicitly distinguishing between surface TEP production and subsurface TEP remineralization when discussing the mechanisms responsible for the observed AOU/nutrient ratios. This distinction is particularly important because TEP production and TEP degradation may influence AOU/nutrient stoichiometry in different directions.
3. Strength of the evidence linking TEP to the observed AOU/nutrient ratios
Another issue concerns the interpretation of the TEP observations. Based on the reported concentrations, the TEP levels observed in this study are generally within the low to moderately low range compared with those reported from the global ocean. Even within the oligotrophic western tropical North Pacific, the measured concentrations appear to be lower than those reported in previous studies, and they are substantially lower than those typically observed in productive coastal regions, frontal systems, or the surface Southern Ocean. Therefore, the statement that TEP-related process is responsible for the observed low AOU/nutrient ratios should be made with greater caution.
In other words, the manuscript currently assumes that TEP abundance is the principal driver of the stoichiometric deviation, yet the observational evidence demonstrates only the presence of TEP rather than an exceptional accumulation relative to other oceanic regions. Therefore, the authors should better justify why relatively modest TEP concentrations are sufficient to produce measurable deviations in AOU/nutrient stoichiometry. Alternatively, the discussion could place greater emphasis on the quality, composition, or turnover of TEP, rather than its absolute concentration, as these characteristics may be more directly linked to remineralization stoichiometry than concentration alone.
Minor or specific:
The reported analytical precision of the POC measurements deserves further clarification. In general, the instrumental precision of an elemental analyzer for carbon determination is typically on the order of approximately 1% under routine laboratory conditions. For real samples, however, the overall analytical precision is usually lower because additional uncertainties are introduced during sample collection, filtration, acidification (or acid fumigation), drying, and other pretreatment procedures. Therefore, the reported analytical precision of 0.8‰ appears to be exceptionally high—nearly two orders of magnitude better than the analytical precision commonly achieved in routine laboratory measurements of marine suspended particulate organic carbon. I am therefore curious about how this level of precision was achieved. Does this value refer to the repeatability of the elemental analyzer itself, the precision of repeated analyses of laboratory standards, or the overall analytical precision including sample pretreatment? Alternatively, could this simply be a typographical error? I recommend that the authors clarify how this value was determined and what it specifically represents.
The description of the TEP analytical method requires clarification. The current protocol omits several key steps of the standard Alcian Blue assay (e.g., staining and washing), making it unclear whether the standard method was actually followed or whether these procedures were inadvertently omitted from the manuscript. In addition, the authors should clarify whether the xanthan gum calibration curve was established under their own experimental conditions or directly adopted from Bittar et al. (2018), as calibration curves are generally expected to be generated within each laboratory to ensure quantitative reliability.
What do the red arrows mean in fig 2a?