Methane stimulates massive nitrogen loss from freshwater reservoirs in India

The fate of the enormous amount of reactive nitrogen released to the environment by human activities in India is unknown. Here we show occurrence of seasonal stratification and generally low concentrations of dissolved inorganic combined nitrogen, and high molecular nitrogen (N2) to argon ratio, thus suggesting seasonal loss to N2 in anoxic hypolimnia of several dam-reservoirs. However, 15N-experiments yielded low rates of denitrification, anaerobic ammonium oxidation and dissimilatory nitrate reduction to ammonium—except in the presence of methane (CH4) that caused ~12-fold increase in denitrification. While nitrite-dependent anaerobic methanotrophs belonging to the NC10 phylum were present, previously considered aerobic methanotrophs were far more abundant (up to 13.9%) in anoxic hypolimnion. Methane accumulation in anoxic freshwater systems seems to facilitate rapid loss of reactive nitrogen, with generally low production of nitrous oxide (N2O), through widespread coupling between methanotrophy and denitrification, potentially mitigating eutrophication and emissions of CH4 and N2O to the atmosphere.

P.7 and Methods p. 14: 'spiked with 15NO3-(plus 14NO2-) and 15NO2-' -this is confusing. Was 14NO2-added? What does it show in contrast to the experiments with 15NO3-and 15NO2-alone? What about background concentrations of nitrogenous compounds? P.7 'It should be noted that almost all of these samples originally contained high CH4 (up to ~34 μM).' This is not high; a lot of lakes reach saturation (around 1500 μM) in anoxic bottom waters.
'Consequently, N2 production rates are expected to be higher in situ.' Why? Didn't you added methane to similar concentrations as in nature? So you hopefully mimick the natural conditions. Here and in other places the results are already discussed. This does make sense, but not if there is also a separate Discussion section. Please restructure. P.8 The entire paragraph Molecular Analysis needs rewriting. Here are my main points of criticism: 'While Type II methanotrophs are generally regarded as more stress-tolerant, those of Type I are usually found in methane-emitting environments with stimulated methanotrophic activity and growth upon nitrogen fertilization (18).' First, being stresstolerant is not in contrast to inhabiting methane-emitting environments. Second, this is again discussion, not presentation of results, and third, this is a very questionable generalization. Even if true, it does not tell anything about the investigated ecosystem. Please correct and rephrase.
The next sentence 'Hence, the detection of particularly Methylomonas-, Methylobacter and Methylocaldum-like pmoA in Markandeya Reservoir likely reflects active methanotrophy therein.' also does not make sense. The detection of genes never tells anything more but the current presence (dead or alive, active or not, having thrived there or higher up in the water column) of a certain group of organisms. 'The pmoA sequences directly related to M. oxyfera were not detected in samples collected in 2011, but some of our retrieved pmoA sequences (e.g. Markandeya pmoA11, pmoA18) are in fact associated with the co-inhabitants of NC10 bacteria (Fig. S9).' Even for an insider this is very difficult to follow. From intensive study of Fig S9 and associated Genbank entries I think the authors mean that some of their sequences are closely related to pmoA sequences of Type I methanotrophs that have been found in the same enrichment culture as NC10 bacteria. But what does that tell, why is it worth mentioning? Also the next sentence is an overstatement; the presence of both methanotrophy and denitrification genes does not corroborate a close association between methanotrophy and denitrification, you will also find those genes in every garden soil or wastewater treatment plant together. 'The genetic capability to reduce nitrite to nitric oxide and/or nitrous oxide is known in several Type I and Type II methanotrophs (ref 19),' -Please discuss in context of more recent literature, eg. Kits et al 2015Kits et al (doi: 10.1111Kits et al /1462Kits et al -2920Kits et al .12772 and doi: 10.3389/fmicb.2015 and Padilla et al 2016Padilla et al (doi: 10.3389/fmars.2017.
'In any case, our detection of both nirS and pmoA in the same water samples supports our observed stimulation of denitrifying activity by methane.' See above; I don't believe there are many environments that do not contain both genes and the detection of genes is of very limited value.
You should also critically address the limitations of the primers you use for nirS, that were partly even known at time of publication (Braker 1998, ref. 39). Since then a vast amount of nirS have been found that are not covered by these primers (see for instance Heylen et al 2006Env. Microb. DOI: 10.1111/j.1462-2920.2006. Very likely, also the denitrifying methane-oxidizing Archaea have nir genes not amplified by these primers. Discussion P. 10 'By contrast, CH4 can accumulate to very high levels (tens to hundreds of μM) in freshwater lakes and reservoirs due to a different production mechanism 22'. Very vague, what does different production mechanism mean? It is both methanogenesis. I think you want to state that there is less competition with sulfate-reducing bacteria for methanogenic substrates. Rephrase. P. 11. Please repeat for clarity what was special in the 2007 incubations.
'It may be noted that the presence of oxygen may also affect functioning of denitrifying methanotrophs but perhaps at higher oxygen levels (ref 30). This may give them an advantage over canonical denitrifiers in shallow systems that are prone to frequent reoxygenation events.' This does not make sense to me. First, ref. 30 used very high O2 concentrations, which are not comparable to the concentrations measured in the deeper waters of the reservoirs. Second, nearly all 'canonical' denitrifiers are facultative aerobes, and consequently only their denitrification enzymes may be damaged, but not the organism as a whole. Additionally, some of the authors themselves have also shown denitrification in presence of oxygen (Gao et al 2010, Aerobic denitrification in permeable Wadden Sea sediments, doi:10.1038/ismej.2010.166). P. 12 'It is not known what fraction of nitrogen is permanently buried in the sediment as opposed to how much is regenerated through respiration …'. I guess you mean aerobic respiration (denitrification is also a type of respiration). Please correct.
Please also rephrase the following sentence 'It is likely that a significant amount of NH4+ in the water column originates from the sediment in addition to DNRA which, as described above, may be important in some cases'.
Please correct n-dano 'Moreover, coupling of anaerobic methane oxidation with NO3-reduction to NO2-by archaea and consumption of NO2-through anammox have also been reported (31)  Anaerobic microorganisms can couple the oxidation of methane to the reduction of sulfate, nitrate and nitrite, iron and manganese oxides. AOM is an important process to reduce the emission of the greenhouse gas methane. The distribution of anaerobic methanotrophs that can couple AOM to nitrate/nitrite reduction in natural environments and their contributions to the global methane and nitrogen cycles are hot research topics attracting a lot of attentions.
This manuscript provides evidences for the existence of methane driven denitrification process in several freshwater reservoirs in India. Overall, I believe their results are sound and important. However, I feel it is not significant enough to be published in Nat Com. Also due to the limitations of experimental plan and methods, some key evidences/results are missing, which reduces the strength of the paper. I will give more detailed comments below.

Significance
In recent years, there are many publications on the distribution of n-damo organisms in fresh water systems and their contributions to methane and nitrogen conversions. For details, see a mini review in EM Report: Nitrate-and nitrite-dependent anaerobic oxidation of methane.
The novelty of this study is that the authors focused on water column, while most of the previous studies targeted sediments. Since it is now an accepted fact that n-damo is a prevalent process in sediments of many different freshwater systems, we would expect it also happens in the anoxic water column above. Therefore, I think this is important results, but not significant enough for Nat Com. I would suggest the authors not only report the existence of methane driven denitrification in these dams, but also quantify and estimate the n-damo activity in these environments (it has been done for the wetland sediments), which will make this paper much more important.

Methodology
Some of the methods used by the authors are classic, e.g. isotopic N measurements. However there are many other aspects could have been better.
To date, there are only two confirmed n-damo microorganisms: M nitroreducens and M oxyfera. The authors tried to detect the key gene for M oxyfera, but not for M nitroreducens. For a paper reporting n-damo activity, this is a serious limitation.
No methane and/to CO2 measurement results was shown. So the paper presents evidences for nitrogen conversion, however there is no conclusive evidence for methane conversion.
Overall, the authors showed that in samples that contains no or very low level of known anaerobic methanotrophs, the addition of methane can greatly enhance denitrification. More efforts should have been made to find out the responsible microorganisms.
No data for other important nutrients. We know AOM can couple to the reduction of sulfate, iron and manganese oxides. Also organic matters can drive denitrification. It is not essential but would be good if the authors can provide the information of these nutrients (in situ concentrations and variations during incubation tests).
Other comments I also feel the manuscript is a bit sloppy. For example, · Typos. n-dano in page 12, compuuted in Fig S2 caption · Sloppy sentences. e.g…More direct chemical evidence has emerged from anaerobic incubations of sediment from Lake Constance14 and of wetland soils in southeastern China10 spiked with 14CH4 and NO2-that led to production of 14CO2…in reference 10 paper, they used 13CH4, not 14CH4. · Strange numbers. 53.2±149.9 nmol, 0.071±0.076 μM; not sure you can get negative values there.
· Use shorthand without defining the full term first, e.g. NIO?? OMZ.

REVIEWER # 1
Reviewer's Comment I have reviewed the paper entitled "Methane stimulates massive nitrogen loss from freshwater reservoirs in India" by Dr Naqvi and colleagues. The authors observed enhanced N 2 production in the presence of CH 4 in hypolimnia of freshwater reservoirs. Water column data, NO 3 reduction processes and CH 4 amendment incubations are presented to support evidence on the coupling between denitrification and methanotrophy. Molecular analysis was also performed. Overall, this is an interesting paper and a valuable addition to a novel research theme, however a few elements should be clearer.

Authors' response
We thank the Reviewer for her/his encouraging and very thoughtful review. We have tried to do our best to address the issues raised by her/him as described below.

1(a). Reviewer's Comment
A large amount of data is presented but, as I understood it, results (from rates/amendments/molecular analysis) were not obtained concomitantly for each sample/site/survey. The range of experimental procedures was not done for the mentioned 8 reservoirs. Even for the more studied reservoir (

Authors' Response
We have expanded the Methods section substantially and included two tables (Supplementary Tables 1 and 2) providing details of dates and measurements made.

Results
Pages 4-5: Was N 2 /Ar measured in several reservoirs? In methods section you stated it was only measured in Markandeya in 04.2015.
Authors' Response N 2 /Ar was measured in 4 reservoirs. Details have been provided in Supplementary Table 1.
We have also plotted data from Tillari Reservoir in Supplementary Fig. 3.

Authors' Response
The new Supplementary Tables 1-3 provide more details than what Table S1 contained.

1(e). Reviewer's Comment
Methods Please add sampling depths or depth intervals.

Authors' Response
Depths of samplings are provided in Supplementary Table 2 and also in the figures.

1(f). Reviewer's Comments
Were there analytical replicates for trace gases/N 2 measurements.
Were there incubation replicates for determination of processes?

Authors' Response
No. The measurements including tracer experiments were made on single samples (now clarified in line 344-345).

1(h). Reviewer's Comments
Are the claims appropriately discussed in the context of previous literature? Yes, although in the meantime I would recommend an additional look for recently published papers.

Authors' Response
We

1(i). Reviewer's Comments
Could the manuscript be shortened to aid communication of the most important findings?
The report on process rates in quite dense and, although important, the detailing is not essential to the major claims of the study.

Authors' Response
We submit that the rates of denitrification, anammox and DNRA, being reported for the first time from any aquatic (freshwater) environment in South Asia, are very important because they are inconsistent with the observed lack of reactive nitrogen accumulation in a region that consumes about one-fifth of the total synthetic nitrogen used globally. Thus, these results indicate a hitherto unrecognized mode of nitrogen loss. We show that the nitrogen loss is driven by methane. However, we accept that the earlier discussion was "dense". We have tried to make it more easily digestible by simplifying and reducing the text and including a table (Table 1).

1(j). Reviewer's Comments
Have they provided sufficient methodological detail that the experiments could be reproduced?
As stated above, I think that methodological detail could be improved. Should the authors be asked to provide further data or methodological information to help others replicate their work? (Such data might include source code for modelling studies, detailed protocols or mathematical derivations). Methods used are not new but additional detail would benefit the Ms.

Authors' Response
We have now expanded the Methods section substantially as suggested by the Reviewer.

REVIEWER # 2 Reviewer's Comments
The paper ‚Methane stimulates massive nitrogen loss from freshwater reservoirs in India ' by Naqvi et al. describes aspects of the nitrogen cycle in these man-made ecosystems using water column measurements, incubation experiments with stable isotopes and PCR-based detection of functional gene markers. Its major novel finding is the stimulation of denitrification by addition of dissolved methane, an observation not previously found for similar ecosystems.

Authors' Response
We thank the Reviewer for her/his encouraging and very thoughtful review. We have tried to do our best to address the issues raised by her/him as detailed below.

2(a). Reviewer's Comments
It remains, however, unclear which organisms and pathways are responsible for this activity.

Authors' Response
In the revision we have attempted to address the Reviewer's concern. Based on the additional data and discussion added to the manuscript we conclude that the CH 4 -dependent production of N 2 from NO 2 is best explained by a diverse denitrifying methanotroph community comprising both NC10 bacteria and conventionally 'aerobic' methanotrophsthe latter of which can either switch to denitrifying mode themselves, or work in syntrophy with other microbes with denitrifying ability including oxygenic nitric oxide dismutation. However, further assessment of single-cell activity and (meta)genomics /transcriptomics analyses are necessary to pinpoint exact nature (single-organism versus syntrophic modes) of the observed denitrifying methanotrophy.

2(b). Reviewer's Comments
The authors also claim to present the largest dataset of nitrous oxide measurements in Indian freshwater bodies, but this is discussed only on the side. The data are relevant for microbiologists and limnologists (and possibly climate modellers, but this is too far from my expertise).

Authors' Response
The N 2 O data set we are presenting is not only the first from any freshwater ecosystem in South Asia, but also the largest from any data set on N 2 O in freshwater in the world, as far as we know. The lack of large N 2 O accumulation is indeed intriguing, given the huge nitrogen loading expected from human activities. Our purpose of including these data here is to make the point that the generally low N 2 O concentrations (only 4% of the values exceeded 100 nM and in a majority of reservoirs the highest concentration was below 25 nM) indicate unusual nitrogen cycling.

2(c). Reviewer's Comments
The paper was difficult to read, it certainly needs improvement in text structure and thorough proofreading by native English speakers. I have commented only on the most disturbing mistakes or unclear sentences.

Authors' Response
We have strived to make the manuscript easier to read. We have restructured it by clearly separating Results and Discussion and bringing the sub-section on N 2 O under the first subsection now titled "Seasonal stratification and its impact on water chemistry". The Discussion part has also been thoroughly revised.

2(d). Reviewer's Comments
Some extra time was unfortunately necessary because it is very unhandy to comment on a version without line numbers.

Authors' Response
We apologize. The revised text includes line numbers.

Authors' Response
We have dropped Reference 7, but have retained Reference 11 as this is the only published report -in a coveted journal -on NC10 bacteria in the water column of a dam-reservoir. The inclusion of latter does not in any way affect our conclusions. The title of the paper by Deutzmann et al. has been corrected (ref 16, line 493). focussed on water columns, which is correct as far as I know, but please be precise.

Authors' Response
We have made suitable changes following the Reviewer's advice (Lines 36-44).

2(g). Reviewer's Comments
Results I do not understand the first subtitle 'Property distribution'. Please clarify.

Authors' Response
The subtitle has been changed to "Seasonal stratification and its impact on water chemistry" (starting line 55) and the previously subsection on N 2 O distribution has also been merged with this subsection. , an intermediate of denitrification. In fact the "secondary nitrite maximum" is invariably associated with the most intense nitrogen loss in the ocean. NO 2 accumulation has also been observed in freshwater systems. In India, hundreds of anoxic groundwater samples we have collected so far invariably contained NO 2 in concentrations of tens of miromol/liter. By contrast, NO 2 concentrations in anoxic hypolimnia are often close to the detection limit and in only 27 cases out of 815 measurements made by us nitrite concentration exceeded 0.5 µM (maximum 1.35 µM). While it is not entirely clear why nitrite accumulates in many denitrifying systems, this is apparently not due to lack of organic substrate because the highest concentrations occur in the most productive systems. We believe the low nitrite concentrations being reported here are significant and intriguing as they are probably related to high CH 4 , which is oxidized by microbes using NO 2 -. We have added three additional references (37-39, lines 543-549) and a brief discussion in response to the Reviewer's comment (lines 271-274).

2(i). Reviewer's Comments
It does not become clear (here or in introduction), why Tillari and Markandeya reservoir were selected for more in-depth study, and generally the choice of reservoirs is not well explained.

Authors' Response
The choice was largely based on logistical convenience -they both are easily reachable from Goa. They also happen to experience different degrees of human impact. We have stated this in the revision (Lines 108-110, 337-341).

2(j). Reviewer's Comments
P.6: This entire page is very difficult to read. Maybe you could partly replace the text by providing a (supplemental) table with an overview of rate measurements?

Authors' Response
We have made suitable changes following the referee's advice. Please see our response to Comment 1(i) for Reviewer #1.

Authors' Response
The ambient nitrite concentrations were very low, as already discussed above. 14 NO 2 was added along with 15 NO 3 to see if 15 NO 2 produced from the reduction of 15 NO 3 was combining with 14 NO 2 to produce 15 N 14 N. As shown in Supplementary Fig. 13, this happens only when CH 4 is present (Clarified in Lines 130-135).

2(l). Reviewer's Comments
P.7 'It should be noted that almost all of these samples originally contained high CH 4 (up to ~34 μM).' This is not high; a lot of lakes reach saturation (around 1500 μM) in anoxic bottom waters. 'Consequently, N 2 production rates are expected to be higher in situ.' Why? Didn't you add methane to similar concentrations as in nature? So you hopefully mimick the natural conditions.

Authors' Response
We agree that CH 4 accumulation in Indian reservoirs is substantially less than in several other reservoirs (which itself is a significant finding that probably reflects greater (anaerobic) methane oxidation). However, the observed concentrations are still three to four orders of magnitude higher than those observed in oxygenated waters and even in many anoxic waters (including the Indian shelf). The point we were trying to make -and apparently did not do a good job in the first instance -is that the samples originally contained CH 4 that would facilitate N 2 production in the natural environment. The dissolved CH 4 was purged out due to pre-incubation sparging with helium and so the controls (which were CH 4 -free) exhibited little production of labelled N 2 . We have now modified the relevant text to make this clearer (lines 141-146).

2(m). Reviewer's Comments
Here and in other places the results are already discussed. This does make sense, but not if there is also a separate Discussion section. Please restructure.

Authors' Response
This is an excellent suggestion. We have followed the Reviewer's advice. The restructured manuscript now does not have much discussion under the "Results" section.

2(n). Reviewer's Comments
P.8 The entire paragraph Molecular Analysis needs rewriting. Here are my main points of criticism: 'While Type II methanotrophs are generally regarded as more stress-tolerant, those of Type I are usually found in methane-emitting environments with stimulated methanotrophic activity and growth upon nitrogen fertilization (18).' First, being stress-tolerant is not in contrast to inhabiting methane-emitting environments. Second, this is again discussion, not presentation of results, and third, this is a very questionable generalization. Even if true, it does not tell anything about the investigated ecosystem. Please correct and rephrase. The next sentence 'Hence, the detection of particularly Methylomonas-, Methylobacter and Methylocaldum-like pmoA in Markandeya Reservoir likely reflects active methanotrophy therein.' also does not make sense. The detection of genes never tells anything more but the current presence (dead or alive, active or not, having thrived there or higher up in the water column) of a certain group of organisms.
'The pmoA sequences directly related to M. oxyfera were not detected in samples collected in 2011, but some of our retrieved pmoA sequences (e.g. Markandeya pmoA11, pmoA18) are in fact associated with the co-inhabitants of NC10 bacteria (Fig. S9).' Even for an insider this is very difficult to follow. From intensive study of Fig S9 and associated Genbank entries I think the authors mean that some of their sequences are closely related to pmoA sequences of Type I methanotrophs that have been found in the same enrichment culture as NC10 bacteria. But what does that tell, why is it worth mentioning? Also the next sentence is an overstatement; the presence of both methanotrophy and denitrification genes does not corroborate a close association between methanotrophy and denitrification, you will also find those genes in every garden soil or wastewater treatment plant together.
'The genetic capability to reduce nitrite to nitric oxide and/or nitrous oxide is known in several Type I and Type II methanotrophs ( 'In any case, our detection of both nirS and pmoA in the same water samples supports our observed stimulation of denitrifying activity by methane.' See above; I don't believe there are many environments that do not contain both genes and the detection of genes is of very limited value. You should also critically address the limitations of the primers you use for nirS, that were partly even known at time of publication (Braker 1998, ref. 39). Since then a vast amount of nirS have been found that are not covered by these primers (see for instance Heylen et al 2006 Env. Microb. DOI: 10.1111/j.1462-2920.2006.01081.x). Very likely, also the denitrifying methane-oxidizing Archaea have nir genes not amplified by these primers.

Authors' Response
This entire section has been rewritten taking into account the Reviewer's comments. We now focus on the new 16S rRNA amplicon sequencing data (instead of functional gene dataset), which gave us an overview of the microbial community structure but with the focus on methanotrophic microbial communities. The dataset -though briefly mentioned before, has been reanalysed against the latest ARB-SILVA data set instead of previously Greengenes, which yielded a lot more robust classification, and also semi-quantitative data to compare community structure at various depths examined. These data are presented in Fig 5 and Supplementary Table 4. Consequently, the criticism from Reviewer on the pmoA and nirS interpretation does not apply any more. Although we still show the pmoA and nirS data in the supplement, they only serve as additional support to the discussion based on 16S data.
More recent publications have been included in the references, including all those suggested by the reviewer.
There are also comments on the limitations the chosen primers in Results section.

2(o). Reviewer's Comments
Discussion P. 10 'By contrast, CH 4 can accumulate to very high levels (tens to hundreds of μM) in freshwater lakes and reservoirs due to a different production mechanism 22'. Very vague, what does different production mechanism mean? It is both methanogenesis. I think you want to state that there is less competition with sulfate-reducing bacteria for methanogenic substrates. Rephrase.

Authors' Response
Thanks. Yes, that is what we meant. We have made suitable changes in the text following the Reviewer's advice (Lines 204-208).

Authors' Response
We have made suitable changes in the text following the Reviewer's advice (Lines 295-299).

2(q). Reviewer's Comments
'It may be noted that the presence of oxygen may also affect functioning of denitrifying methanotrophs but perhaps at higher oxygen levels (ref 30). This may give them an advantage over canonical denitrifiers in shallow systems that are prone to frequent reoxygenation events.' This does not make sense to me. First, ref. 30 used very high O 2 concentrations, which are not comparable to the concentrations measured in the deeper waters of the reservoirs. Second, nearly all 'canonical' denitrifiers are facultative aerobes, and consequently only their denitrification enzymes may be damaged, but not the organism as a whole. Additionally, some of the authors themselves have also shown denitrification in presence of oxygen (Gao et al 2010, Aerobic denitrification in permeable Wadden Sea sediments, doi:10.1038/ismej.2010.166).

Authors' Response
We are, of course, aware of the Gao et al. (2010). However, we point out that there is overwhelming evidence that oxygen inhibits N-loss in water column when present even in traces (sub-micromolar concentrations) in areas such as the Bay of Bengal and Gulf of California. And while many of the denitrifiers may be facultative and genetically equipped to carry out denitrification the denitrifying genes do not seem to be expressed in the presence of traces of oxygen. What we are proposing is that low denitrification activity in the Indian reservoirs in the absence of CH 4 could be because the O 2 concentrations are often kept above that threshold (functional anoxia) as in many oceanic oxygen minimum zones. By contrast denitrifying heterotrophs that are actually postulated to produce O 2 may have a higher tolerance for O 2 . However, in view of the Reviewer's criticism we have rephrased the text aprropriately (Lines 278-286).

2(r). Reviewer's Comments
P. 12 'It is not known what fraction of nitrogen is permanently buried in the sediment as opposed to how much is regenerated through respiration …'. I guess you mean aerobic respiration (denitrification is also a type of respiration). Please correct. Please also rephrase the following sentence 'It is likely that a significant amount of NH 4 + in the water column originates from the sediment in addition to DNRA which, as described above, may be important in some cases'.

Authors' Response
We have made suitable changes following the Reviewer's advice (Lines 305-311).

2(t). Reviewer's Comments
'Moreover, coupling of anaerobic methane oxidation with NO 3 reduction to NO 2 by archaea and consumption of NO 2 through anammox have also been reported (31).' It would be logical to first mention that NC10 bacteria and archaea have been found several times together (

2(u). Reviewer's Comments
Methods P. 15 Please check language in last sentence.

Authors' Response
Done. Fig S7: I do not have a good alternative suggestion, but this is a difficult-to-grasp figure, because the several hundred cases on the right side are graphically not represented, only coded in the legend.

Authors' Response
We have removed the Figure and included a Table (Supplementary Table 4) listing the same data.

REVIEW # 3 Reviewer's Comments
This manuscript provides evidences for the existence of methane driven denitrification process in several freshwater reservoirs in India. Overall, I believe their results are sound and important. However, I feel it is not significant enough to be published in Nat Com. Also due to the limitations of experimental plan and methods, some key evidences/results are missing, which reduces the strength of the paper. I will give more detailed comments below.

Authors' Response
We thank the Reviewer for her/his encouraging and in-depth review. We also thank her/him for pointing out the errors that had unfortunately crept into the initial submission. We have tried to do our best to address the issues raised by her/him.

3(a). Reviewer's Comments
The novelty of this study is that the authors focused on water column, while most of the previous studies targeted sediments. Since it is now an accepted fact that n-damo is a prevalent process in sediments of many different freshwater systems, we would expect it also happens in the anoxic water column above. Therefore, I think this is important results, but not significant enough for Nat Com. I would suggest the authors not only report the existence of methane driven denitrification in these dams, but also quantify and estimate the n-damo activity in these environments (it has been done for the wetland sediments), which will make this paper much more important.

Authors' response
While thanking the Reviewer for her/his appreciation of the significance of our work, we agree that while quantification of methane-driven denitrification in freshwater systems will be the next logical step, at this point we are hesitant to scale up our results because of insufficient data.

3(b). Reviewer's Comments
Methodology Some of the methods used by the authors are classic, e.g. isotopic N measurements. However there are many other aspects could have been better. To date, there are only two confirmed n-damo microorganisms: M nitroreducens and M oxyfera. The authors tried to detect the key gene for M oxyfera, but not for M. nitroreducens. For a paper reporting n-damo activity, this is a serious limitation.

Authors' response
We submit that the lack of information on M. nitroreducens is not a serious limitation. This is because while M. nitroreducens does oxidise methane anaerobically, it only reduces NO 3 to NO 2 -. It does not produce N 2 on its own. Therefore it is not correct to consider M. nitroreducens a (nitrite-driven) N-DAMO organism like NC10 bacteria. Consequently, our observed CH 4 -stimulated N 2 production from NO 2 cannot be due to M. nitroreducens as suggested. In comparison, many of the 'aerobic' Type I-III methanotrophs have various nitrogen reducing activities and they contribute almost 14% relative abundance in our samples.

3(c). Reviewer's Comments
No methane and/to CO 2 measurement results was shown. So the paper presents evidences for nitrogen conversion, however there is no conclusive evidence for methane conversion.

Authors' response
We submit that while double labelling experiment would have demonstrated consumption of CH 4 , we can think of no explanation of the effect observed by us other than CH 4 oxidation by NO 2 -. Moreover, CO 2 may also be produced by other oxidants such as sulphate, Mn (IV) and Fe (III), present in our samples, and also by nitrate reducers that only produce NO 2 -(e.g. M. nitroreducens) but not gaseous nitrogen forms. The absence of stimulation of N 2 production by CH 4 in this coastal marine environment, where CH 4 concentrations remain very low even during anoxic periods (Naqvi et al., 2010) also shows that the effect observed by us is not an experimental artefact and is linked to the availability of CH 4 .

3(d). Reviewer's Comments
Overall, the authors showed that in samples that contains no or very low level of known anaerobic methanotrophs, the addition of methane can greatly enhance denitrification. More efforts should have been made to find out the responsible microorganisms.

Authors' response
We agree. However, we submit that our observation of low numbers of NC10 bacteria is by itself quite significant because it implies that the community is more diverse than recognized so far. We show that the other denitrifying methanotrophs considered to be 'aerobic' are very abundant in anoxic waters and should play an important role in nitrogen loss.

3(e). Reviewer's Comments
No data for other important nutrients. We know AOM can couple to the reduction of sulfate, iron and manganese oxides. Also organic matters can drive denitrification. It is not essential but would be good if the authors can provide the information of these nutrients (in situ concentrations and variations during incubation tests).

Authors' response
While we agree the AOM is known to be coupled to the reduction of sulphate, iron and manganese, this study focuses on CH 4 -driven denitrification, and not on AOM (please also see our response under 3b above). In fact, we have recorded high concentrations of iron and manganese in Tillari Reservoir, but we are not including these data as they do not provide any insight into the process we are investigating.

3(f). Reviewer's Comments
Other comments I also feel the manuscript is a bit sloppy. For example, Typos. n-dano in page 12, compuuted in Fig S2 caption Authors' response Corrected.

3(g). Reviewer's Comments
Sloppy sentences. e.g…More direct chemical evidence has emerged from anaerobic incubations of sediment from Lake Constance 14 and of wetland soils in southeastern China 10 spiked with 14 CH 4 and NO 2 that led to production of 14 CO 2 …in reference 10 paper, they used 13 CH 4 , not 14 CH 4 .

Authors' response
We regret the error. The statement has been corrected.

Authors' response
The high standard deviation arises from the wide range of values. It does not imply negative rates.

3(k). Reviewer's Comments
Wrong figure caption or legends, e.g. Fig S2, legend should be NO3+NO2? Fig S6, caption suggest ammonium data will be presented, but not in the figure.
I have now evaluated the revised manuscript by Dr Naqvi and colleagues. The authors addressed the comments and suggestions of the reviewers and the manuscript is much improved. Results and Discussion sections are more clear. Methods section is improved but the described addition treatments don´t match those described in the Results so please revise. I trust the manuscript is acceptable for publication following some minor corrections.
Specific notes: Line 65: "was" instead of "is". Please check if the past tense is used throughout the presentation of results.
Line 93-94: "815 measurements" of what? Please include the measured variable in the sentence.
Lines 117-118: How high was NH4+ in the samples where rates were measured? The presence of 14NH4+ will result in diluted isotopic labeling and bias the estimation of anammox.
Line 124: In the Methods section you state that DNRA was only measured in samples incubated with 15NO2-.
Lines 130: Again, the amendments don't match the stated in Methods section.
Lines 133-134: The isotope pairing technique is based on this assumption, if this wasn't true, 15N incubation experiments would simply not be used. I agree with reviewer 3 that this amendment doesn't add much information.
Line 136: Figure 2 is not related to what is stated in the sentence.
Line 138: Did you calculate anammox in these incubations? In Figure 4 the production of 14N15N also increases which might suggest enhanced anammox since ambient NO3-+NO2-at that depth is too low (Fig. 2) for 29N2 to be produced through denitrification.
Line 211: methanotrophic Line 247: "nod gene has been detected also in the proteobacterium HdN1, along with a number of contaminated aquifers and wastewater treatment systems". Please rephrase Line 365: you can also measure anammox from the incubations with just 15NO2-when ambient 14NH4+ is present, as appears to be the case with your samples. The quality of this manuscript has been improved significantly after revision. The initial version contained some errors, which are fixed now. Restructuring the manuscript and using table to replace text description make it much more reader-friendly, especially the methodology section. More upto-date literature are also included now. The authors have given satisfactory answers to the majority of issues raised by the reviewers.
Reviewer #4 (Remarks to the Author): In the manuscript "Methane stimulates massive nitrogen loss from freshwater reservoirs in India" the authors describe a large dataset on concentrations and distribution of nitrogen species in reservoirs all across India. In addition, the authors collected a large dataset on N2 formation rates in these reservoirs. The finding of methane significantly increasing denitrification rates is novel and has to my knowledge not been reported before.

General comments
The comments of reviewer 2 have been addressed suficiently.
Are Indian reservoirs nitrogen limited or phosphate limited? Which element determines the trophic status of freshwater in this case?
I agree with reviewer 2 that the identity of the organisms performing methane induced denitrification is missing. However, I understand that elucidating the identity of these organisms is not in the scope of this publication and would require a lot of work and time. On the other hand, I cannot follow the argumentation by the authors why classical methanotrophs or NC10 bacteria are supposed to carry out the observed denitrification. There are many questions that the authors could have addressed/discussed with the data they have available: -Are the numbers of NC10 bacteria sufficient to explain the observed denitrification rates based on literature values of cellular activity? -Is there evidence that the classical methanotrophs described to switch to denitrification can perform n-damo? -Was methane consumed stoichiometrically with denitrification rates? -Based on the substrate gradients measured on many occasions: is there evidence for significant n-damo insitu?
In addition, a PCR based survey for the cited nod genes in the samples the authors collected could well be within the scope of this publication and shed light into the denitrification pathway at play in these reserviors.
The profiles showing the distribution of nitrate/nitrite, ammonium, methane and oxygen indicate pronounced ammonia oxidation/nitrification (or leftover oxidized nitrogen species from the last mixing event, if not in steady state). Did you include nitrification measurements? How much N2O do you expect based on ammonia oxidation?
Better comparison to "usual" concentrations (and mentioning typical ranges in similar habitats) would be helpful in all the instances where the authors describe concentrations measured in this study as "unusually low" or use other comparative expressions. How much N2O is usually formed for a given denitrification rate? L129: what do you mean with "apparent inadequacy"? Can you provide data that the measured rates are not sufficient to explain the low concentrations?
L136: What was the DOC in these samples? Is methane the only possible electron donor?
Your experiments are perfect to analyze incorporation of 15N or 13CH4 and to do nano-SIMS analysis paired with FISH to identify the organisms that are active.
L187: Figure 1 shows nitrate depletion throughout the water column in spring/early summer. In this case "the very low concentrations of oxidized nitrogen forms in anoxic hypolimnia" can result from the absence of nitrate in the first place. However, I agree that for the profiles you show in Figure 2, the explanation you provide is very likely. Please specify.
L191: please provide reference values for this comparison.
L202: The pathway of nitrogen loss might be the same or similar. The organisms and the coupling to the electron donor might be different. Please be more concise.
L219: another explanation for the presence of aerobic methanotroph in anoxic environments is sedimentation. Aerobic methanotrophs have been found and isolated from anoxic environments repeatedly. It would be surprising if all of them thrived on n-damo.
L137: without additional evidence I would prefer a phrase like "…methylotrophs could potentially also contribute…" L148: For a high impact publication I would have expected that the authors screen genomes and amplify the nod gene from their samples to provide additional evidence that this process plays a significant role here.
L256: You discuss that NC10 might be important (0.003-0.022% of sequences) but exclude significant anammox with (<0.013%) of the reads. Please provide a reasoning why similarly abundant microbes play a role or not or report a value better suitable for this statement.
L259ff: The community does not HAVE to rely on M. nitroreducens like archaea, but is could still be an option. All the statements following this sentence do not exclude significant participation of M. nitroreducens in the process.
L298: the stratification in 2010 shown in Fig 1 seems to be very stable. Did you see a prevalence of canonical denitrification in these samples to corroborate your statement?
Supplementary table 3: These data are interesting, but in the current form useless for the reader. Because all data of one location are mixed, it is not possible to see whether NO2-is present in anoxic or oxic parts and where N2O was measured.
Supplementary figure 4: Same as in 3: the information is useless, because all samples might be reported here and denitrification is not expected in some of them, e.g. oxic samples. What is this table supposed to show?
Supplementary figure 4 & 5: These figures look very messy. Even with colors, it is not easy to distinguish the different profiles, especially the low concentrations.