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?

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:

1. 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.
2. 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.
3. 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 NO_3meas is defined as the sum of NO₃-N and NO₂-N concentrations, please refer to it as NO_x.

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.

I think the authors have replied all my comments and I have no further questions on this manuscript.