In this manuscript, the authors report nitrous oxide production pathways in two eutrophic reservoirs using ¹⁵N tracer incubations, natural-abundance isotopes, and functional gene quantification. The methodologies are well-established and proven effective in clarifying nitrous oxide production in aquatic systems; the datasets add valuable observations to the community; and the analyses generally support the claim that denitrification dominates water‑column nitrous oxide production. The manuscript is suitable for target journal when properly revised. Note: line numbers and pages from authors’ PDF file.

My main concern is in the title. The authors argue that denitrification could be the predominant process regulating nitrous oxide production, and in the Discussion section, the authors present evidence about higher nirS abundance and isotopic patterns associated with denitrification. However this argument may be weakened by the fact that, denitrification was generally absent at the oxygenated surface water (figs. 2 & 3), and the N₂O consumption potential inferred from natural abundance isotopic data. The authors acknowledged that nosZ was quantified only at the deepest depths (n=4) and therefore cannot constrain N₂O reduction within the entire reservoir (line 270–275; p.12 figure caption). I suggest the authors reframe the argument/statement to better characterize the novelty of their work.

Some minor comments below:

Line 31 – 33: These global estimates of increased N2O emissions from inland waters are often with large uncertainties. Better to state as “mean ± uncertainty”

Line 35 – 37: There are increasing number of literatures about GHG emission from reservoirs (doi: 10.5194/bg-11-5245-2014; 10.1016/j.watres.2025.123420; 10.3390/su132111621 )

Line 52 – 54: Should clarify about low but not zero oxygen promoting partial denitrification and thus net N2O production.

Line 103: Filtrate passing through 0.7 μm GF/F filter may not be suitable to characterize DOC; 0.45μm filter is recommended.

Line 110 – 120: Should mention the pore size of filter collecting molecular samples. Because genetic materials were collected from water pre-filtered through 3 μm, there may be bias toward underestimating particle‑attached nitrifiers or denitrifiers (as stated line 370 – 371).

Line 122: It is better to specify the criteria for selecting the three depths in the main text. And specify when the N2O concentration or isotope samples were measured at which facility. Preservation using mercuric chloride is generally not recommended for sample storage longer than 1 year.

Line 124: What was the volume of air headspace during oxic incubation?

Line 186: It seems the incubation timepoints for nitrification were different from those of N2O production; which two time points were analyzed for 15N-nitrate?

Line 152: The equation (1) by Santoro et al. will overestimate the N2O production from ⁴⁶N₂O signal. The equation proposed by Ji et al., 2018 GBC (doi: 10.1029/2018GB005887) is recommended.

Line 183 – 190: This section 2.8 about calculating N2O yields using two equations, (4) & (5); which one is used to represent data described in line 240 & 246?

Line 191 – 202: Authors should clarify the consistent amount of N injected into mass spectrometry to determine natural abundance. This is important because the concentrations of N species varied with depth. If varying amounts of N were injected, even for the same water sample, mass spectrometry will yield varying isotopic values.

Line 212: Apparently high DO at the surface (> 400 micromolar, ~2-fold saturation) suggests a very strong oxygen source that can only be supported by blooming algal activity. This was not evident from the chl-a concentration profiles (10 – 20 microgram per liter);

Line 318–323: The main text should clarify “sample #12 excluded as specified in the caption of Fig. 6f”

(as stated in caption L325–333).

Line 335 & 466: I am not sure about the statement “remove significant amount of N”. There could be possibility about the loss of nitrate due to algal assimilation, and the biomass being exported to the sediment. In addition, statements about reservoir‑level DIN loss described in Section 4.4 and the supplementary lack uncertainty estimates and assumptions (depth weighting, temporal representativeness, varying hydraulic retention time, etc). Please add a short paragraph enumerating assumptions and explain the possible caveats. Readers may realize that these DIN loss potential could be specific to the sampling period (Jul–Sep), not necessarily annual rates (L465–474 & Table 2).

Line 362 – 365: Authors should clarify the inconsistencies about anoxic depths with measurable amoA gene abundance (fig 3b), or ammonium oxidation rates (fig 2a).

Line 374 – 375: Where are the data for ammonia oxidation/nitrification, that can infer comammox?

Line 444: Are the authors suggesting denitrification potential in anoxic water column or the sediment? Please clarify.

Line 452 – 465: It is better to address the exact profiles shown in figures 2 & 3 when discussing oxycline turnover times and hypolimnetic storage, to help readers understand the statements.

General Comment

This study aims to investigate N₂O production in two reservoirs and to distinguish its origin between nitrifying and denitrifying pathways. To achieve this, the authors combine natural-abundance isotopic analyses with rate measurements of N₂O production associated with partial and complete nitrification as well as denitrification, together with molecular tools to quantify and trace the relevant metabolic pathways at the genetic level. The authors find that denitrification appears to be the main source of N₂O, with consistently higher N₂O production rates and gene abundances than those associated with nitrification. The results highlight the value of combining isotopic and molecular approaches to understand nitrogen cycling in aquatic systems. The methodologies applied are well established. Overall, the manuscript addresses a timely and important topic in the context of climate change and contributes new insights into the origin of N₂O production in lakes. The text is generally well written, although I suggest a minor reorganization of some sections to improve the flow (see specific comments below).

Specific Comments

Materials and Methods

1. Reorganization of isotopic abundance section: I suggest moving the section on natural isotopic abundances so that it follows immediately after the “Vertical profiles and biogeochemical characterization” section and precedes the “Functional genes” section. Because isotopic abundances are part of the chemical characterization of the water column, presenting them earlier would improve the logical flow of the manuscript. If this restructuring is adopted, the corresponding results section should be reorganized accordingly, presenting the natural isotopic abundance results right after the physicochemical characterization and before the genetic characterization. While not essential, I believe this change would strengthen the overall structure.
2. Subsection “Statistical tests”: I recommend renaming this subsection to “Data analysis”, which would allow the authors to describe more clearly the analytical criteria and tools used (e.g., the numbering system in the figures, the δ¹⁸O:δ¹⁵N ratio, etc). Please also provide additional detail regarding the statistical procedures applied to linear and non-linear regressions. I assume that assumptions of normality, homoscedasticity, and independence were evaluated. Additionally, please specify the significance threshold used (e.g., p < 0.05).

Technical Comments

Line 90: Please could you provide more detail on where and how the vertical profiles were measured? How many profiles were obtained per reservoir and sampling date? Was the same sampling site used in July and September?

Line 118: Please specify which nosZ clade (I or II) was quantified.

Line 124: Which was the headspace volume used for the oxic samples? Please, indicate it.

Line 212: A concentration >800 µmol O₂ L^-1 is unusually high (>25 mg O₂ L⁻¹) … Considering the DO profiles shown, it may be worth double-checking the calculation. For instance, if 16 mg O were used instead of 32 mg O₂ for the conversion, this could partly explain the discrepancy. I kindly suggest verifying this value to ensure consistency.

Figure 1a: All N₂O concentration points for the Cubillas reservoir are the same color (orange). Additionally, the negative sign is missing from “-25” on the x-axis of the ¹⁵N–NO₂^- panel.

Line 244: Please review spacing between symbols and values here and throughout the manuscript.

Line 248: Please could you clarify more explicitly that these samples were excluded from the analysis?

Line 256: Since there is no statistically significant relationship between the two variables, please reconsider the use of the word “coupled.” “Accompanied by” would more accurately describe the pattern.

Lines 257–258: The formula and interpretation of NO₂^- turnover time (and N₂O turnover time) would be more appropriately placed in the Methods section rather than in the Results. Including this information earlier would help readers better follow the analyses and their interpretation.

Line 261: Consider using p > 0.05 for non-significant results, and report exact p-values only when results are marginally significant. (Same comment for lines 269, 270, and 275.)

Figures 2 and 3: What do the numbers displayed next to N₂O concentrations represent? Please clarify this in the figure caption. The colour coding is also confusing: orange is used both for July samples and for N₂O production, regardless of sampling date. Please consider selecting a different colour for N₂O production.

Line 290: The dark-gray sediment colour referenced in the caption is not visible in any panel of Figure 3. Please remove this part of the caption.

Figure 4: Please consider using a lighter colour (or open symbols) for the excluded data points. As currently displayed, they are somewhat difficult to distinguish.

Figure 5: Please explain what the numbers represent, ideally in the caption. Additionally, clarifying in the Methods how these numbered points relate to those in Figures 2 and 3 would help guide the reader through the Results and Discussion.

Figure 5a: Why is the segment connecting points 11 and 12 shown in red? I could not find an explanation in the text.

Figure 5c: There appear to be two red dotted lines. Which one is valid? Could you please specify and clarify this in the caption? I additionally suggest explaining the use of this ratio more clearly in the “Data analysis” section.

Line 314–315: Please could you provide a reference for the threshold defining suboxic conditions (DO < 10 µmol L^-1).

Line 317: The manuscript uses the term “relationship” for nirS vs. DO concentration, but “correlation” for nirS  vs. cumulative Chl-a. Please use consistent terminology throughout.

Line 367–368: Given the lack of detection issues for AOA in the Cubillas reservoir in September, I am not fully convinced that the presence of AOB and Comammox can be dismissed as easily.

Line 375–376: Because no positive control for Comammox was available, the absence of amplification does not allow the rejection of the hypothesis that high nitrification rates without ammonium oxidation could be due to complete ammonia oxidation. I encourage the authors to consider this possibility.

Line 411–412: If the earlier suggestion is incorporated, this description should be moved to the “Data analysis” section.

Line 415: To support the interpretation, “which indicates net N₂O production” should specify by which process (i.e., denitrification, AOB, or Comammox).

Lines 417–418: The term “coupling” implies a relationship between variables that is not statistically supported. Please consider using “accompanied by” instead.

Lines 432–440: These results are very interesting, and the discussion provided here is excellent!