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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Status: open (until 24 Jul 2026)
- RC1: 'Comment on egusphere-2026-2947', Anonymous Referee #1, 28 Jun 2026 reply
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- 1
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?