The paper «A potential explanation for the anomalously low nitrate to phosphate ratio in the well-oxygenated East/Japan Sea » by Kim et al. attempt to explore the contribution of bacterially mediated N loss for explaining the low N:P ratio encountered in the East/Japan Sea. The study is based on the hypothesis that N reducing pathways, i.e. nitrate reduction and denitrification, may occur at relevant magnitude in their study area (despite the well oxygenated conditions encountered), enough to explain low NO3-PO4 ratios. To test their hypothesis, the authors use sequencing data from samples collected between the surface and 1000 m depth during 5 cruises in the EJS, between February and October 2021. 16S sequencing was used to build up a taxonomic classification of bacterial communities at the order level. Furthermore, they applied a computational tool to infer functional properties of the obtained bacterial communities in an attempt to analyse the relative abundance of N-reducing genes.

I am not a specialist in genomics approaches but (or maybe because of that) I find that the Methods section lack literature references (with doi) for applied protocols, bioinformatics tools/pipelines and used databases. Hopefully, other reviewers more proficient in the field may assess whether the used methodology is sound.

This said, the main and critical caveat of this work is, in my opinion, that the conclusions are not supported by the data and the interpretation of the results is sometimes way too speculative. The authors base their conclusions in a series of numbers (percentages of N-reducing genes and associated bacterial communities) which do not give sufficient quantitative information. Throughout the manuscript, the authors state that they found « high » abundances of N-reducing genes ; but high compared to what ? And how can we know that the obtained percentages are « enough » to explain the observed N:P ratios ? Moreover, seasonal and vertical variability is presented without really assessing the reasons and consequences of this variability.

Nutrient data collected during the cruises are exploited only superficially although they should be at the center of their study. In the current version, all nutrient data have been merged to produce a unique value of NO3:PO4 ratio which is not presented in the results section but in the introduction. I strongly suggest to present the nutrient profiles for each cruise to explore seasonal and vertical variability in the same way as the genomics data. This may allow to compare the variability between nutrients and genomics data which may help assessing the role of N-reducing pathways in N loss in the water column.

The Results and Discussion section reads more like a literature review of the factors that may drive N:P ratios in the study area and I found that the results are not discussed enough. Moreover, there are a number of inconsistencies in the arguments given. For instance, the first part of the section claims that external phosphorus inputs are insufficient to explain low N:P ratios but later on, the authors state that N-enriched atmospheric deposition is responsible for high N:P ratios in surface waters. Again, presenting nutrient profiles will be very useful to understand whether N:P ratios are indeed higher in the surface that in deeper waters.

All the above are suggestions to help the authors derive clear findings from their hypotheses and data, and present substantial scientific insights. I suggest a thorough revision of the paper, particularly the Results and Discussion section, but I must say that I am not sure if such a thorough revision will finally make the manuscript suitable for publication in Biogeosciences.

Specific comments:

Lines 57-59. If low N:P ratios are a known feature of the EJA, I suggest the authors refer to literature data in the introduction and present their own data in the results section in a more detailed way.

Lines 64-66. Since genomics-based techniques are experiences rapid advances, the authors may want to cite more recent references.

Line 81. I guess it was filters and not filtered samples that were frozen and used for DNA extraction.

Line 83. Same comment as above.

As said before, the results and discussion section is awkward. Indeed, only 3.2. sub-section is properly results and a bit of light discussion. Sub-section 3,1 reads more like a literature review.

Lines 139-140. Please, add references for the selected biomarker genes.

Figure 2. Is there a possibility of adding error bars?

Line 169. Aren’t some of these orders (e.g. Alteromonadales, Pseudomonadales) ubiquitous in the ocean?

Line 178-179. The statement that proportions of 37.7% of N-reducing genes and 20.0% of taxa indicate the potential for bacterially mediated N loss is not very convincing. How these numbers compare with other regions?

In this manuscript, Kim et al. explore the possible causes for the relatively low NO3:PO4 ratio in a well-oxygenated water column in the East/Japan Sea. They collected water samples from different depths over five months to understand microbial N cycling. They measured the abundance of N-reducing genes and the distribution of functionally grouped N-reducing bacterial communities. Based on these (non-quantitative) sampling results, they conclude that there is dual feedback driving the low NO3:PO4, i.e., enrichment in NO3 due to atmospheric N deposition and reduction of NO3 in low-oxygen microenvironments. They conclude that in the future, this process will prevail, as subsurface N removal associated with climate-driven deoxygenation, and the EJS can potentially serve as a sentinel for biogeochemical response in other regions. 

Major comments

Overall, the paper is well written and clear. However, I think that the evidence given in the manuscript does not justify the conclusion. First, the water column in the EJS is well oxygenated (Fig. 1B). So, even a proposed reduction in 20 M O₂ will not make the deep ocean anoxic. Therefore, the proposed dual-scale feedback seems to be irrelevant to the EJS. 

The author also mentions in the abstract that low NO3:PO4 in the well-oxygenated EJS is a “long-standing biogeochemical enigma”. This is the first time I have heard of this interesting enigma, and I would like to understand more about how past studies have approached it. The authors only provide a general statement (“Much of our current understanding of marine N cycling ...”  LN 50). It is missing to understand what has been done until today.

P-balance: The riverine P balance has not been sufficiently analyzed. I would like to get more quantitative information about the riverine input – when was the dam constructed? What is the NO3:PO4 in the CDW? What do you mean by “confined to surface layers”? It is possible that the low NO3:PO4 is due to past influx? I would like more quantitative information on the long-term NO3:PO4 balance for the EJS. Furthermore, what about the release of P from anoxic sediment?

I am not so familiar with the sequencing protocol, so I am unable to evaluate it. However, to gain more quantitative intuition into the significance of the N-reducing genes, it would be beneficial to compare them with other locations. Perhaps other studies showed the relationship between N-reducing genes and rates? 

Is it possible to plot NO3:PO4 vs. depth?

Minor comments

line 35 - > cite Tyrell ‘The relative influences of nitrogen and phosphorus on oceanic primary production’ (1999)

Line 50 -> cite Martiny et al., ‘Strong latitudinal patterns in the elemental ratios of marine plankton and organic matter’, 2013.

Line 50: What do you mean by “circulation terminates”?

Line 60: “Much of our current understanding of marine N cycling...” is it a general statement or is it specific to the EJS?