This manuscript presents an interesting and detailed study on the benthic nitrogen cycling in the Santa Barbara Basin. The study is original as the authors used a complex approach measuring in-situ incubation, quantifying benthic rates of nitrate uptake, denitrification, anammox, nitrous oxide production, and DNRA. They found that the sediments in the Santa Barbara Basin acted a sinks for fixed nitrogen with dominating denitrification and as source for nitrous oxide. The data set is well presented and interpreted and the text well written and organized. I only have a few minor comments.

L141-142: How big is the effect of additional substrate added to chamber incubations? In-situ bottom water concentrations ranged from 9.9 µmol L^-1 to 27.3 µmol L^-1 (Table 1), after adding ¹⁵N-labeled nitrate concentration varied between 50 and 100 µmol L^-1. Do you suspect to overestimate rates to higher substrate availability?

L256-257: How would rate changes with seasonal altering oxygen concentrations?

L258-259: How representative are the results considering seasonal changes in oxygen and nitrate concentrations?

L297 “However, because the porewater NH₄⁺ concentration was high […]”: Have pore water or bottom water ambient ammonium concentrations been measured? I cannot find any information about porewater sampling in the method section. If you refer to another paper this statement needs a reference. Both anammox and nitrification, which according to the authors contributes at least in part to N₂O production (L367), are dependent on available ammonium, it would be interesting to know the in-situ concentrations.

L364-370: Why do you not discuss the potential of DNRA to contribute to N₂O production?

General comment

The authors investigated nitrogen cycling using in-situ incubations with the addition of ¹⁵NO₃^- in the deep Santa Barbara basin, which is mainly anoxic. During incubations, the benthic uptake of total nitrate (NO₃^-), denitrification, anaerobic ammonium oxidation (anammox), dissimilatory nitrate reduction to ammonium (DNRA) and N₂O production were assessed. 

I agree that such incubations are challenging, but they provide new information on rates. In reality, the present contribution provides information about one more new study site using benthic chambers. At the same time, there are also many limitations to using the isotope pairing method during chamber incubations for studying sedimentary dissimilatory pathways. These limitations could be better addressed in the present study. 

Regarding benthic dissimilatory pathways, questions still need to be answered about whether the study underestimated ^29/30N₂ and ¹⁵NH₄⁺ production rates since samples were only collected from the water phase. Conventionally, NO₃^- reduction rates are based on production rates in both the bottom and pore water phases. Additional explanations help address this point. Secondly, I am concerned about the time period that needs to reach diffusion equilibrium after the ¹⁵NO₃^- addition.

Also, I suggest a strongly revised discussion. At the present version of the manuscript, I could not recommend it for publication in BG.  My specific and general comments are provided below.

Specific comments

Line 29-30: what do you mean here, "feedback loop"?

Line 34-35: this is entirely speculative as the reader can not see by which magnitude benthic processes could affect bottom/water concentrations of NO3 and N2O. The water column is quite high, and what proportion of the standing pool could be affected?

Line 57:  what can lead to an increase in oxygen levels during incubations? Please clarify if the C: N ratio provided is molar. Consider adding subscripts for TOC and TON to understand better how they refer to sediments. 

Line 85-90: the authors state what they did, which sounds quite descriptive. What was the motivation and aim of this study? I suggest providing questions that the authors aim to answer.

Line 139-144: please provide the final enrichment degree achieved. Maybe I am less familiar with chamber operation, but I need more explanation of how IPT assumptions were achieved during these chamber incubations (for e.g. D14 rates independence of 15N additions (I guess here authors used only D15 rates), equilibrium in diffusion etc.)

Line 169-171: here, the authors state that the production of ^29/30N₂ was calculated from linear regression; however, looking at the text related to the incubations, it seems they sampled once per incubation. Then, this is quite confusing.

Line 197-232: section 3.1 aims to argue that the technique used did not underestimate measured rates. Overall, this section should be better developed.

Lines 205-207: the authors recognize the weaknesses of the approach used. However, they need to identify what could potentially lead to 

underestimation. 

Line 207: there appears to be a sudden jump in the logical flow. 

Lines 219-223: need more concrete arguments regarding whether rates were underestimated.  

Line 222: the authors say that parallel incubations were performed, but I could not find this information in the Materials and Methods.

Line 225: the authors should have discussed intracellular storage in the introduction to clarify their meaning. 

Lines 297-299 need to be clarified on where the data presented comes from.

Line 338-340:  this is quite a speculative statement.

Line 385-398: this is quite a speculative statement without supportive information.

Line 423-434: in this section, authors should avoid the reption of results.

Technical comments

Table 1: The measures in the first column could be clearer, and it is challenging to understand which numbers are for the sediment or water column.

Figure 2 is quite complex and needs to be reshaped. I suggest providing the total N2 production and the partition between different dissimilatory pathways. Another option is to provide total nitrate reduction and partitioning between different pathways. I was surprised standard error bars are shown here without clarity on replication. Therefore, Table 2 could be modified.