Nitrous oxide as a function of oxygen and archaeal gene abundance in the North Pacific

Oceanic oxygen minimum zones are strong sources of the potent greenhouse gas N2O but its microbial source is unclear. We characterized an exponential response in N2O production to decreasing oxygen between 1 and 30 μmol O2 l−1 within and below the oxycline using 15NO2−, a relationship that held along a 550 km offshore transect in the North Pacific. Differences in the overall magnitude of N2O production were accounted for by archaeal functional gene abundance. A one-dimensional (1D) model, parameterized with our experimentally derived exponential terms, accurately reproduces N2O profiles in the top 350 m of water column and, together with a strong 45N2O signature indicated neither canonical nor nitrifier–denitrification production while statistical modelling supported production by archaea, possibly via hybrid N2O formation. Further, with just archaeal N2O production, we could balance high-resolution estimates of sea-to-air N2O exchange. Hence, a significant source of N2O, previously described as leakage from bacterial ammonium oxidation, is better described by low-oxygen archaeal production at the oxygen minimum zone's margins.

Trimmer et al. explore potential drivers of the production of nitrous oxide [N2O] in low-oxygen [O2] waters of the Eastern Tropical North Pacific oxygen minimum zone. They use a combination of O2 manipulation experiments using isotopic labeling, rate measurements, and marker gene counts to inform and parameterize a non-linear mixed effects model that shows a strong exponential relationship between declining O2 and increasing N2O and a significant positive correlation with counts of the Archaeal marker gene nitrite reductase (AnirK). Significant negative relationships between O2 and N2O concentrations have been described previously in ocean OMZ regions. Such patterns have been used to suggest a role for nitrifiers in ocean N2O production, either directly via chemical decomposition of ammonia oxidation intermediates, or via so-called nitrifier-denitrification, in which ammonia oxidation to NO2 is coupled to NO2 reduction by the same organism. Here, through some of the first experiments to test the N2O and O2 relations, the authors observe an excess of single 15N-labeled N2O in incubations with 15NO2 coupled with a strong positive relationship between AnirK abundances and N2O production rates, and use these results to implicate Archaeal nitrifier-denitrification as the most likely source of N2O. Overall, this is a comprehensive, statistically robust, and well-conceived study that provides strong support for the hypothesis that ammonia-oxidizing Archaea play an important role in N2O production. Broadly, these results will be useful for helping constrain models to determine effects of O2 content on greenhouse gas cycling.
There are, however, several issues that deserve attention prior to publication.
1) Gene/cell counts data not well described, and questionable. Why are AnirK counts 2 orders of magnitude higher than those of AamoA (~106 vs 104 per ml) if both genes are putatively localized in the same organism)? Indeed, Figure 4 shows maximum AnirK counts of ~5,000,000 per ml, with an average closer to about 200,000 per ml (~ln 12). Frankly, these values seem high to me. Is 10^6 AnirK per ml consistent with AOA abundance in this system (or in comparison to other systems; e.g., ETSP), and with knowledge of nirK copy number in available Thaumarchaeota genomes? Of course, the magnitude of difference between AnirK vs AamoA counts cannot be explained by copy number variation alone. Is it possible that the AnirK primers are non-specific and that the qPCR assays are also amplifying denitrifier nirK? Or something else? (Was there any attempt to confirm the specificity of these primer sets for this study?) Some (rough) insight into this these questions could presumably come from the counts of total Marine Group I (MGI) 16S copies (Table S5), although these data are not presented (why???), or by considering prior literature on correlations among MGI 16S, AamoA, and AnirK genes (e.g., e.g., Lund et al. 2012, ISME find a much smaller difference in AamoA vs AnirK counts). These questions are important for validating the integrity of AnirK as a marker for Archaeal ammonia oxidation.
2) Per-cell rates? A more transparent discussion of the gene count data could be used to help bound per-cell estimates of N2O production (based on the experimental incubations). Doing so would be useful, at the very least for determining whether the observed rates, if they are not realistic at the per-cell level based on knowledge from the literature, could be driven partly by other processes. 6) Treatments/levels need more explanation. Notably, the treatment names "N2, N2O, N2O + O2, etc" (see Table 1) are not well described. As a consequence, the first mention of "12 experiments" (line 109) is somewhat baffling. Please briefly clarify (in the Results) the overall experimental plan. 7) Target depths. Following on comment #6, the main text does not actually specify the two target depth zones from which samples were collected. Indeed, this information is cryptic even in the Methods at the end of the manuscript. Please clarify. 8) Chemical concentrations/context. The Intro would benefit from additional details regarding the environmental conditions/significance of the target study area. How much N2O production is actually associated with OMZs ("significant sources" in line 30 is vague, and not further qualified)? From prior work, how much N2O is present? What are the "representative oxygen concentrations" referred to in line 76? 9) "Bottle effects" (lines 123-12129) discussion unclear. Bottle effects can mean a variety of things. Please clarify the exact bias or pattern being tested for here, and how time series sampling is helping rule out such effects. 10) qPCR standard curves. I did not see a description of how the standard curve for the qPCR assays was generated. Specifically, what was the source of standard template DNA?
Line 108. Should "dual labeled" instead be "single labeled"? (based on data elsewhere in paper; e.g., lines [204][205][206][207] Line 125. What is the "main" experiment? Reviewer #2 (Remarks to the Author): Review MS NCOMMS-16-03439 General Comment: Trimmer et al. present results on nitrous oxide (N2O) production as a function of dissolved oxygen availability in the 1 to 30 um range and archaeal gene abundance in the North Pacific. This is a careful study that focuses on the mechanistic basis for production of nitrous oxide in low-oxygen marine environments. This is an important and unresolved problem in the marine nitrogen cycle research and of potential interest to a broad audience. Overall, the manuscript is well written and organized. Field based measurements of nitrous oxide concentrations, isotopic signatures, and substrates utilized to facilitate its production are relatively scarce in oceanic environments, and the data are valuable.
However, the interpretation of the mechanism used to produce nitrous oxide by ammonia-oxidizing Thaumarchaea needs to be re-assessed, considering the recent findings that incorporate the production and evolution of "nitric oxide (NO)" by ammonia oxidizing archaea (see below).
Specific Comments: 1. Two recent publications (Martens-Habbena et al. 2015;Kozlowski et al. 2016) using pure cultures of marine and terrestrial Thaumarchaea (Nitrosopumilus maritimus SCM1 and Nitrosophaera vienesis) have provided evidence for "nitric oxide" as an important intermediate produced by both organisms. The production of nitrous oxide by ammonia-oxidizing Thaumarchaea was conceptualized based on a side reaction involving nitric oxide produced by the ammoniaoxidizing organism that was subsequently converted to nitrous oxide by "a reaction with water". While the most convincing of these studies utilized a soil isolate, the central biochemistry is conserved among both isolates, and genes and transcripts associated with these reactions are often detected in metagenomic and metatranscriptomic surveys. The essential inhibition of nitrification in isolates and coastal marine waters with a nitric oxide scavenger, PTIO, provides further support for this mechanism.
Reviewer #3 (Remarks to the Author): The paper reports an extensive biogeochemical and microbiological study of rates and pathways of N2O formation in the world's largest oxygen minimum zone (OMZ), concluding that N2O production can be ascribed to ammonium-oxidizing Archaea through coupled nitrificationdenitrification, and that rates can be predicted from a simple oxygen dependent rate expression. OMZs are recognized as important sources of atmospheric N2O, but there is no consensus on the mechanisms and regulation of N2O production there. Thus, if the conclusions hold, the study represents a substantial step forward, which should be of interest to a wide audience.
The strengths of the study include the high spatial coverage and large experimental dataset of good quality. As stated in the paper, it is the first detailed experimental investigation linking N2O production under in situ conditions to a specific microbial pathway. In its present form, however, a number of issues appear to undermine the central conclusions.
1) The reported 15N-N2O production rates greatly underestimate total N2O production. N2O production rates are based on incubations with 15N-labeled nitrite, a central finding being that the 15N-labeled N2O formed is mainly of mass 45 (15N14NO) rather than mass 46 (15N15NO) as would be predicted from the isotopic composition of nitrite. This leads to the (correct) conclusion that N2O is mainly stems from another source than nitrite and (l. 208) that the majority of N in N2O is actually 14N -which implies that most of the N2O produced during the experiments accumulated as 44N2O (14N14NO). Based on the relative accumulation of masses 45 and 46 (Fig.  2c), typically {greater than or equal to} 50:1 but highly variable, and assuming random isotope pairing during the denitrification step to N2O, we can estimate that total 44N2O production rates in the experiments were typically at least 10 times higher than 15N-N2O and that this factor varied strongly between individual experiments (the situation is analogous to the use of the isotope pairing technique to quantify denitrification in aquatic sediments where a large fraction of N2O/N2 is formed through coupled nitrification-denitrification). This has serious implications: Firstly, the correlations of N2O production to oxygen, gene numbers, etc., must apply to the total rates (or 44N2O rates) and not only to the 15N-N2O rates as demonstrated now. It is not clear if this will be the case, because each data point should be scaled individually depending on the 45N2O/46N2O production ratio. Secondly, the rate expression used for modelling should also be based on total rates. As far as I can see, increasing the rates by an order of magnitude will lead to a similar increase in the modelled N2O concentration (Fig. 5), which means that the model will no longer fit the measurements. The experimental dataset needs to be re-evaluated.
Furthermore, it should be acknowledged that the experiments are, presumably, blind to "leaky" nitrifier N2O production through the hydroxylamine pathway. Thus, total N2O production could be even larger that what the calculations mentioned above will show. This could have been investigated by measurement of N2O production in the 15N ammonium incubations, which were included in the study. Did the authors attempt such measurements?
2) The archaeal nirK gene numbers appear orders of magnitude too high. The central conclusion that N2O is produced through archaeal nitrification-denitrification rests strongly on the correlation of rates and AnirK gene numbers determined by qPCR. These numbers are extremely high (Fig.  S5), up to 10^6 mL-1, which is similar to or higher than total prokaryote counts in mesopelagic waters, and 2 orders of magnitude higher than the counts of archaeal amoA genes in the same samples. While the cells may have more than one copy of each gene, it is unlikely that they have 100 copies of nirK. Furthermore, a previous study (Lund et al. 2012) found a reasonable agreement between AnirK and AamoA in North Pacific waters, and typical numbers of 10^4 mL-1, in agreement with the AamoA counts here and in another study from the same OMZ (Beman et al. 2012, L&O). This discrepancy might suggest that the nirK primer set as applied here is not specific for thaumarchaeotal ammonium oxidizers, which clearly undermines the conclusion based on the correlation.
3) The background of the paper, as presented here, is a bit of a strawman. The authors argue that the present understanding is that N2O formation in OMZs is due to bacterial ammonium oxidizers. This is an out-dated point of view, which originates from the days before the role of Thaumarchaeota was realised. Studies by Francis, Beman, Stewart and others have clearly documented that bacteria play a very minor role in the ammonium oxidizer community and in ammonium oxidation in OMZs, and Santoro and coworkers have shown that Thaumarchaeota are a likely source of N2O there, and that at least part of their N2O production is through nitrificationdenitrification. The novelty of the present story lies in the experimental approach and derivation of quantitative relationships, not in discovering the role of Thaumarchaeota.

Specific comments
19: through 550 km is not informative specify inshore-offshore gradient or similar 21: strong 45N2O signature makes no sense without explanation of the methods 46: here and in many other places the authors use quotation marks in an unclear manner -does this indicate dubious results or what? 48: explain "N2O anomaly" 64: Thaumarchaeota is used elsewhere and should be correct 87: unclear sentence -how can the MLD extend to 25 m and then increase steadily? 92: what is "the true anoxic core"?? 93: unclear: nitrite and N2O minima were found at 350 m and occurred at 400-450 m?? Fig. S2 is very difficult to understand. Why are the same data points shown in multiple frames in both a and b? Why do the sections overlap sometimes but not always? 107: is there such a thing as O2-free nitrogen gas? (and OFM is used but not defined anywhere) 108: dual labelled 45N2O?? 120: exponential increase is confusing without stating the direction of oxygen concentrations -it is an exponential decrease with increasing oxygen 121: it is not obvious to me that the exponential function is consistent with the in situ distribution 124: these developments are by no means "approximately linear". Two out of four clearly cease completely after 12 h, and the two others clearly decelerate after 20 h -the effect seems to be depth dependent. The underestimation of rates in the long incubations adds further uncertainty to issue #1 above. 200-2: please explain -why does the fact that nitrification is active lead the authors to expect no N2O production from nitrite? Nitrifier denitrification depends on nitrification. 209-11: the relevance of this sentence is not clear. 225-6: the authors did not measure net nitrification (i.e. increase in concentrations of nitrite+nitrate), I believe. Furthermore, Kalvelage and coworkers have reported nitrate reduction to 20 µM oxygen in OMZ waters, so why would 1 µM exclude the process? The potential for nitrate being the source of 14N in N2O should be discussed further. 228-9: what does "and, though not directly" mean? 240-1: this is pure speculation -being better adapted doesn't mean being perfect 260: Babbin did not present a variant of the authors' model -it is the other way around 276-8: this seems to contradict the general applicability of the simple model advocated earlier 281-2: air-sea exchange rates should be independent of the assumptions about pathways of N2O production? 320: how were vials filled with He is they were only sealed later? 442: where does the Heaviside function come from? The data implies increasing N2O production all the way to zero oxygen. What does a* refer to -it is not in the equation? (here again, why the quotation marks? Fig. 1: Specify definitions of the OMZ boundary and N deficit. It would be useful to have different markers for the different stations in c) and d).  Table S2: The explanation of the rates is highly confusing. According to methods, nitrite oxidation was apparently from incubations with 15N nitrite. If nitrification is the sum of ammonium and nitrite oxidation, how can the values be lower than nitrite oxidation? Table S5: Where are the results from the quantifications of non-candidate genes (bacterial 16S RNA etc.)? What is the justification for the choice of AnirK primers All 3 reviewers highlighted issues with the qPCR data. We reviewed the data and the methods used to collect it. In doing so it quickly became apparent that the PDRA who did the analyses had made some significant, and somewhat bizarre errors in her determination of the gene copies in the standards used in these qPCR assays. These included errors associated with poor DNA quantification but also a failure by the PDRA to do simple calculations properly. Given these issues we have gone back to the raw data and recalculated everything from scratch again, ensuring these were correct this time. This has altered all the counts and produced much lower counts for general bacterial 16S and AnirK such that there is now a much closer correlation between AamoA and AnirK counts (ratio AnirK:AamoA mean = 1.98, median = 0.41) and far better agreement with previous counts of these genes in other aquatic environments. We have also sequenced AnirK PCR products from these samples and they are overwhelmingly most closely related to other AnirK sequences, which we have now reported in the manuscript. Therefore we are confident that these data are now correct, that our analysis is specific for AnirK and so the questions raised by both Reviewer 1 and 3 about possible amplification of non-AnirK genes we think are no longer a concern.
Reviewer 1 also suggested that AnirK may not be an effective marker for ammonia oxidation. AnirK is a marker for nitrite reduction leading to the production of N 2 O NOT for ammonia oxidation and our sequence data validates the PCR we have used as an effective method to analyse this gene. However, the most important point is that the abundance of this gene, and AamoA, is correlated with N 2 O production. These correlations support our suggestion of AOA nitrifier-denitrification as the source of N 2 O as our work has shown it cannot be produced by canonical denitrification or, indeed, bacterial ammonium oxidation.
Reviewer 2 suggests that using transcript analysis may improve our linkage between the activity of AOA and N 2 O production. However, analysis of mRNA from natural samples is very challenging and the relationship between transcript copy number, translated protein copies and activity is very difficult to define effectively for model organisms in the laboratory, let alone environmental organisms in situ (see. Pedneault et al. 2014Scientific Reports 4 4661: Taniguchi et al. 2010. Gene abundance is an effective proxy for cell numbers and does show correlation to activity in our analysis, which is exactly what would be expected and therefore we cannot see how an RNA-based analysis is likely to clarify the message we are presenting. The reference to Stewart et al. 2012 seems odd to us as this was a purely molecular analysis without any process measurements at all. Whilst it shows that gene and transcript abundance are variable (across many genes) it cannot show which is a better measure of an organism's contribution to an actual process in situ.

Point by point to each reviewer. Reviewer #1 (Remarks to the Author):
Trimmer et al. explore potential drivers of the production of nitrous oxide [N2O] in low-oxygen [O2] waters of the Eastern Tropical North Pacific oxygen minimum zone. They use a combination of O2 manipulation experiments using isotopic labeling, rate measurements, and marker gene counts to inform and parameterize a non-linear mixed effects model that shows a strong exponential relationship between declining O2 and increasing N2O and a significant positive correlation with counts of the Archaeal marker gene nitrite reductase (AnirK). Significant negative relationships between O2 and N2O concentrations have been described previously in ocean OMZ regions. Such patterns have been used to suggest a role for nitrifiers in ocean N2O production, either directly via chemical decomposition of ammonia oxidation intermediates, or via so-called nitrifier-denitrification, in which ammonia oxidation to NO2 is coupled to NO2 reduction by the same organism. Here, through some of the first experiments to test the N2O and O2 relations, the authors observe an excess of single 15Nlabeled N2O in incubations with 15NO2 coupled with a strong positive relationship between AnirK abundances and N2O production rates, and use these results to implicate Archaeal nitrifier-denitrification as the most likely source of N2O. Overall, this is a comprehensive, statistically robust, and well-conceived study that provides strong support for the hypothesis that ammonia-oxidizing Archaea play an important role in N2O production. Broadly, these results will be useful for helping constrain models to determine effects of O2 content on greenhouse gas cycling.
There are, however, several issues that deserve attention prior to publication.
1) Gene/cell counts data not well described, and questionable.
Why are AnirK counts 2 orders of magnitude higher than those of AamoA (~106 vs 104 per ml) if both genes are putatively localized in the same organism)? Indeed, Figure 4 shows maximum AnirK counts of ~5,000,000 per ml, with an average closer to about 200,000 per ml (~ln 12). Frankly, these values seem high to me. Is 10^6 AnirK per ml consistent with AOA abundance in this system (or in comparison to other systems; e.g., ETSP), and with knowledge of nirK copy number in available Thaumarchaeota genomes?
Please see the response to qPCR and molecular analysis above Of course, the magnitude of difference between AnirK vs AamoA counts cannot be explained by copy number variation alone. Is it possible that the AnirK primers are non-specific and that the qPCR assays are also amplifying denitrifier nirK? Or something else?
Please see the response to qPCR and molecular analysis above (Was there any attempt to confirm the specificity of these primer sets for this study?) Some (rough) insight into this these questions could presumably come from the counts of total Marine Group I (MGI) 16S copies (Table S5), although these data are not presented (why???), or by considering prior literature on correlations among MGI 16S, AamoA, and AnirK genes (e.g., e.g., Lund et al. 2012, ISME find a much smaller difference in AamoA vs AnirK counts).

The MG1 and general bacteria (mentioned by Reviewer 3) data are not used at all
in the manuscript because they add nothing to our analysis or understanding of the production of N 2 O in these waters. However, with our reanalyzed qPCR data these data are broadly similar to AamoA and AnirK counts in these samples and to illustrate this we have added a comparative figure to the Supplementary Information (Fig S6) that is cited in the results. Line 158.
These questions are important for validating the integrity of AnirK as a marker for Archaeal ammonia oxidation.
Please see the response to qPCR and molecular analysis above 2) Per-cell rates? A more transparent discussion of the gene count data could be used to help bound per-cell estimates of N2O production (based on the experimental incubations). Doing so would be useful, at the very least for determining whether the observed rates, if they are not realistic at the per-cell level based on knowledge from the literature, could be driven partly by other processes.

Even though this issue is probably linked to the errors in our original count data it is a good suggestion and would confirm that our data lie with a range that is supported by previous work. The per cell rate for the N 2 O production rates we measure at oxygen concentrations below 30µM is 2 or 5 attomol N 2 O per copy (cell) h -1 for AnirK and AamoA respectively. Shaw et al. (Environ. Microbiol. 2006) report 2-58 attomol N 2 O per cell h -1 for Nitrosospira. We have added a couple of lines into the text to report this and there is no need to invoke "other processes" as suggested by the reviewer. Lines 175-179.
3) N2O production mechanism. It remains unclear how AOA generate N2O from NO2.
Many AOA genomes, including several from marine environments, encode only nirK, and those AOA genomes that do encode components of downstream denitrification steps are missing key catalytic subunits (e.g., of nitric oxide reductase). Given this lack of mechanistic understanding, the extent to which AnirK may a priori be considered a reliable proxy for AOA-based N2O production is (seemingly) debatable. The choice of AnirK as a marker, and the state of knowledge about the NO2-to-N2O production step should be briefly discussed (building upon the brief mention in line 239).
It is true that it is unclear how AOA generate N 2 O from nitrite, but with the presence of AnirK it is clear these organisms can reduce nitrite, presumably to NO. The failure to detect other denitrification genes has to be seen in the context of just how different archaeal genes are from bacterial homologs. AamoA is really quite different from bacterial amoA so the issue here (no clear nitric oxide reductase-type gene) may well be due to gene divergence between the archaeal and bacterial clades. What is clear is that N 2 O production from AOA is common, and supported as a process in situ by Santoro's work and from a molecular standpoint by Lund et al., whose primers we have used. Thus, AnirK has good provenance in the literature as a marker for AOA N 2 O production. The Kozlowski paper mentioned by Reviewer 2 below does suggest that the pathway to N 2 O in AOA may be distinct from a classic bacterial nitrifier-denitrification route. However, that does not alter the story we present here nor the data we present in Figs 3, 4 and 5. 4) "Experimental component" could be better articulated/emphasized in the Intro. It took a second reading to realize that the paper was trying to draw attention (e.g., in para 2 of the Intro, para 1 of the Discussion) to the fact that this work is one of the first (the first?) studies to show the inverse relation between N2O and O2 using "experiments", rather than environmental data. I know that this is stated in the Intro, but it is done in such a way as to be easily overlooked (it happened in my first reading of the ms, so it is possible for others as well). To better highlight this novel aspect of the work, I suggest moving some of the stronger statements from lines 246-249 into the Intro. This will immediately establish a contrast to prior work.
That's a great idea, thanks. See new and edited lines 42 to 61.

5)
Nitrite/ammonia oxidation rates. It would be useful to provide a brief mention of how the measured rates compare (consistent/inconsistent?) to those previously observed in the eastern Pacific (e.g., Beman et al. 2012, Kalvelage et al. 2013, Ganesh et al. 2015.

The comparison with measurements by Kalvelage 2013 is made on line 229
; yes it is very brief but supplemental measurements of nitrification are not our focus and we are tightly constrained by space.
6) Treatments/levels need more explanation. Notably, the treatment names "N2, N2O, N2O + O2, etc" (see Table 1) are not well described. As a consequence, the first mention of "12 experiments" (line 109) is somewhat baffling. Please briefly clarify (in the Results) the overall experimental plan.
Yes this was inadequate. We now describe our experimental design briefly at the start of the results section -Nitrous oxide production as a function of oxygen-See lines 106-110 and have fully revised the description of the treatments in Table 1. 7) Target depths. Following on comment #6, the main text does not actually specify the two target depth zones from which samples were collected. Indeed, this information is cryptic even in the Methods at the end of the manuscript. Please clarify.
We have clarified this as part of point 6 above. Our aim was to generate natural variation in both ambient oxygen and nitrous oxide concentrations which we largely achieved. 8) Chemical concentrations/context. The Intro would benefit from additional details regarding the environmental conditions/significance of the target study area. How much N2O production is actually associated with OMZs ("significant sources" in line 30 is vague, and not further qualified)? From prior work, how much N2O is present? What are the "representative oxygen concentrations" referred to in line 76?
The first thing to say of course is that the amount of N 2 O production associated with OMZs remains rather uncertain and maybe why most papers tend to shy away from explicitly assigning a value, instead opting for vague terms such as "major" or "substantial". We have included a reference and given a range for global OMZs N 2 O emissions of 0.8-1.35 Tg N yr -1 compared to an oceanic total of 1. 8-5.8, i.e. OMZs roughly in the range 20-75% of the oceanic N 2 O total (and excluding coastal ecosystems). We have also included a value for oxygen under which N2O shows strong accumulation (<62.5µmol 1 -11 ) where N 2 O is known to accumulate, keeping it as brief as possible in both cases, see lines 30 and 78. 9) "Bottle effects" (lines 123-12129) discussion unclear. Bottle effects can mean a variety of things. Please clarify the exact bias or pattern being tested for here, and how time series sampling is helping rule out such effects.
Yes it was unclear. We merely wanted to check if our 72h incubation overestimated production, as some related work with 15 N-N 2 has suggested that it might. Work with 15 N for N 2 production by anammox or denitrification uses regression of production over time but these studies are usually only interested with measuring N 2 under ambient conditions and reporting those observations. Here we wanted to experimentally test the effect of oxygen on N 2 O but a combination of the large 1L glass-vials and multiple oxygen treatments precluded a full time series incubation in each of the 12 main experiments with N 2 O by oxygen treatment i.e. 1400 1L bottles versus our 280. We did measure its production at 2,4,9,18,36 and 72h at two oxygen saturations and for two depths to check that production was approximately linear (Fig. S4). Clearly production wanes after 18 h but where it was strongest and most linear (90m) the rates recorded ~30 nmol m -3 d -1 and 56 nmol m -3 d -1 are representative of our overall median value of 58nmol m -3 d -1 . At 60 m production was weak and markedly non-linear over 72h but not representative of our main data set at ~8nmol m -3 d -1 . Note, that the total amount of N 2 O varied significantly across the 12 main experiments i.e. the deviation in the random intercept in Fig. S5 but this is captured by the mixed effects model which does a good job at parameterising the 1D model (Fig 3 and 4 Line 125. What is the "main" experiment?
Redundant and removed.

Reviewer #2 (Remarks to the Author):
General Comment: Trimmer et al. present results on nitrous oxide (N2O) production as a function of dissolved oxygen availability in the 1 to 30 um range and archaeal gene abundance in the North Pacific. This is a careful study that focuses on the mechanistic basis for production of nitrous oxide in low-oxygen marine environments. This is an important and unresolved problem in the marine nitrogen cycle research and of potential interest to a broad audience. Overall, the manuscript is well written and organized. Field based measurements of nitrous oxide concentrations, isotopic signatures, and substrates utilized to facilitate its production are relatively scarce in oceanic environments, and the data are valuable.
However, the interpretation of the mechanism used to produce nitrous oxide by ammoniaoxidizing Thaumarchaea needs to be re-assessed, considering the recent findings that incorporate the production and evolution of "nitric oxide (NO)" by ammonia oxidizing archaea (see below).
Specific Comments: 1. Two recent publications (Martens-Habbena et al. 2015;Kozlowski et al. 2016) using pure cultures of marine and terrestrial Thaumarchaea (Nitrosopumilus maritimus SCM1 and Nitrosophaera vienesis) have provided evidence for "nitric oxide" as an important intermediate produced by both organisms. The production of nitrous oxide by ammoniaoxidizing Thaumarchaea was conceptualized based on a side reaction involving nitric oxide produced by the ammonia-oxidizing organism that was subsequently converted to nitrous oxide by "a reaction with water". While the most convincing of these studies utilized a soil isolate, the central biochemistry is conserved among both isolates, and genes and transcripts associated with these reactions are often detected in metagenomic and metatranscriptomic surveys. The essential inhibition of nitrification in isolates and coastal marine waters with a nitric oxide scavenger, PTIO, provides further support for this mechanism.
We are a little confused by this point and hope we can clarify. As stated above the actual pathway of N 2 O production in AOA is still not clear but both of the mentioned papers support a role for NO in Thaumarchaeal metabolism, which in no way negates anything we say. In fact, NO is implicit in our argument that N 2 O production is in part explained by Anirk abundance, as we would expect this archaeal analogue of nirK to code for a nitrite reductase whose product would indeed be NO. Here, variation in the abundance of AnirK and AamoA correlates with N 2 O production. We added 15  2. While gene abundances were used in this study to explain the nitrous oxide signals, utilization of transcript would be more convincing, and perhaps yield more explanatory power over genes abundances alone. This is especially true for marine Thaumarchaea, which often display high activities at the base of the oxycline, but are often at abundance levels that are considerably lower. The metatranscriptomic analysis of the eastern tropical South Pacific oxygen minimum zone by Stewart et al. (2012) is an example that displays the mismatch between gene abundance and activity quite well.
Please see the initial response above 2. The choice of oligo-nucleotide primers used to assess the abundance of the amoA gene corresponding to both Bacterial and Thaumarchaeal groups is a bit surprising, given that both are utilized primarily in terrestrial environments, and the later is considerably degenerate.

(Minor) L128 "
The overwhelming majority of studies have argued for nitrification by ammonia oxidizing bacteria ..." This is a weak and old argument by now.
The statement was redundant as it is covered at the end of the discussion section where we characterize our source of N 2 O and to save space it has been removed from the discussion. This general line of argument was also raised by Reviewer 3 and we justify the structure of our introduction there in some detail, but in essence we seek to address the assumptions of a wide variety of potential readers, including the oceanographic community which has yet to assimilate the nuanced arguments within the microbial ecology community about the differences between AOA and AOB and their relative importance in N 2 O production. Thus we present this entrenched, but recently challenged view that oceanic N 2 O is produced by oxygen-stressed AOB. This is essential to properly place our work into a broad scientific context rather than assuming that a role for AOB has been conclusively disproven in the minds of all of our potential readers. Paragraph 2 and 3 within the Introduction do exactly this and we absolutely emphasise the now recognized importance of AOA over AOB in an OMZ. See paras 2 and 3 of the Introduction and lines 216 where this text has been removed but is now summed up on line 259-260.

Reviewer #3 (Remarks to the Author):
The paper reports an extensive biogeochemical and microbiological study of rates and pathways of N2O formation in the world's largest oxygen minimum zone (OMZ), concluding that N2O production can be ascribed to ammonium-oxidizing Archaea through coupled nitrificationdenitrification, and that rates can be predicted from a simple oxygen dependent rate expression. OMZs are recognized as important sources of atmospheric N2O, but there is no consensus on the mechanisms and regulation of N2O production there. Thus, if the conclusions hold, the study represents a substantial step forward, which should be of interest to a wide audience.
The strengths of the study include the high spatial coverage and large experimental dataset of good quality. As stated in the paper, it is the first detailed experimental investigation linking N2O production under in situ conditions to a specific microbial pathway. In its present form, however, a number of issues appear to undermine the central conclusions.
1) The reported 15N-N2O production rates greatly underestimate total N2O production. N2O production rates are based on incubations with 15N-labeled nitrite, a central finding being that the 15N-labeled N2O formed is mainly of mass 45 (15N14NO) rather than mass 46 (15N15NO) as would be predicted from the isotopic composition of nitrite. This leads to the (correct) conclusion that N2O is mainly stems from another source than nitrite and (l. 208) that the majority of N in N2O is actually 14N -which implies that most of the N2O produced during the experiments accumulated as 44N2O (14N14NO). Based on the relative accumulation of masses 45 and 46 (Fig. 2c), typically (greater than or equal to) 50:1 but highly variable, and assuming random isotope pairing during the denitrification step to N2O, we can estimate that total 44N2O production rates in the experiments were typically at least 10 times higher than 15N-N2O and that this factor varied strongly between individual experiments (the situation is analogous to the use of the isotope pairing technique to quantify denitrification in aquatic sediments where a large fraction of N2O/N2 is formed through coupled nitrification-denitrification). This has serious implications: Firstly, the correlations of N2O production to oxygen, gene numbers, etc., must apply to the total rates (or 44N2O rates) and not only to the 15N-N2O rates as demonstrated now. It is not clear if this will be the case, because each data point should be scaled individually depending on the 45N2O/46N2O production ratio. Secondly, the rate expression used for modelling should also be based on total rates. As far as I can see, increasing the rates by an order of magnitude will lead to a similar increase in the modelled N2O concentration (Fig. 5), which means that the model will no longer fit the measurements. The experimental dataset needs to be re-evaluated.
We think there's just been a simple mistake here. The reviewer begins by stating that "Based on the relative accumulation of masses 45 and 46 (Fig. 2c) We have, however, extended our calculations (equ. 3,4&5) in the methods (lines 365-390) to estimate total N 2 O production from the total 14 N and 15 N-NO 2 pool to make our data comparable to those working more frequently with 15 N and the production of N 2 but not as the reviewer suggested. We now use the complete form of the widely published calculations for estimating total rates of N 2 production by anammox and denitrification 1 and no longer just report the 15 (Fig. 4) are also unaffected and these new parameters have no effect on the output of the 1D model (Fig. 5).

Method lines 365-390.
Furthermore, it should be acknowledged that the experiments are, presumably, blind to "leaky" nitrifier N2O production through the hydroxylamine pathway. Thus, total N2O production could be even larger that what the calculations mentioned above will show. This could have been investigated by measurement of N2O production in the 15N ammonium incubations, which were included in the study. Did the authors attempt such measurements? The reviewer may have had a valid point here if we had any evidence of a significant contribution from AOB in these samples, which we do not. Furthermore, the Martens-Habbena and Kozlowski papers referred to by Reviewer 2 shows a clear role for NO in AOA ammonia oxidation but one that is clearly distinct from any role NO may have in AOB. Therefore, it is very unlikely that leaky nitrifier N 2 O is confounding our analysis in this study.
Please also note -that neither of the two concerns raised by the reviewer here would have any effect on either our revised or original story. We experimentally manipulated oxygen and directly measured an exponential increase in 15 N-N 2 O. The residual variation that couldn't be explained by oxygen correlates with archaeal gene abundance. Also, parameterizing a 1D model with our non-linear model coefficients reproduces the pattern of N 2 O in the ocean (incredibly well!) and, with that model, we can balance direct estimates of air sea exchange -the issues raised by this reviewer do not change any of that.
2) The archaeal nirK gene numbers appear orders of magnitude too high. The central conclusion that N2O is produced through archaeal nitrification-denitrification rests strongly on the correlation of rates and AnirK gene numbers determined by qPCR. These numbers are extremely high (Fig. S5), up to 10^6 mL-1, which is similar to or higher than total prokaryote counts in mesopelagic waters, and 2 orders of magnitude higher than the counts of archaeal amoA genes in the same samples. While the cells may have more than one copy of each gene, it is unlikely that they have 100 copies of nirK. Furthermore, a previous study (Lund et al. 2012) found a reasonable agreement between AnirK and AamoA in North Pacific waters, and typical numbers of 10^4 mL-1, in agreement with the AamoA counts here and in another study from the same OMZ (Beman et al. 2012, L&O). This discrepancy might suggest that the nirK primer set as applied here is not specific for thaumarchaeotal ammonium oxidizers, which clearly undermines the conclusion based on the correlation.
Please see the response to qPCR and molecular analysis above 3) The background of the paper, as presented here, is a bit of a strawman. The authors argue that the present understanding is that N2O formation in OMZs is due to bacterial ammonium oxidizers. This is an out-dated point of view, which originates from the days before the role of Thaumarchaeota was realised. Studies by Francis, Beman, Stewart and others have clearly documented that bacteria play a very minor role in the ammonium oxidizer community and in ammonium oxidation in OMZs, and Santoro and coworkers have shown that Thaumarchaeota are a likely source of N2O there, and that at least part of their N2O production is through nitrification-denitrification. The novelty of the present story lies in the experimental approach and derivation of quantitative relationships, not in discovering the role of Thaumarchaeota.
As we state above in response to reviewer 2 there is still a substantial community of oceanographers and ocean modelers who have not assimilated the rapidly evolving ideas about AOA and AOB in ocean nitrogen cycling. As our data will be a challenge to the well-established view of many researchers in this field we absolutely have to address the idea that AOB drive N 2 O production in the oceans absolutely head on. However, we also focus a significant proportion of the original introduction on highlighting the growing recognition of the role that the archaea are playing in the production of N 2 O including half of the references cited here. The intro starts with a broad and simple overview of N 2 O in the ocean -and the multiple microbial metabolisms that may play a role. We then explore the thickening of OMZs and recognize that the perspective of ocean modelers is that N 2 O is largely due to bacterial ammonia oxidation. The final section brings the story up to date by bringing in the archaea (which is the reviewer's point above but it is not widely known to all with an interest in N 2 O) and finish by simply stating that "There has, however, been no formal experimental characterisation of N 2 O production at oxygen concentrations representative of the margins of an OMZ and/or the abundance of AOA (or any other candidate organism) in representative samples of the ocean 2 . Here we provide experimental evidence…." We attempted to set the scene from all angles to broaden the appeal of our paper.

Specific comments
19: through 550 km is not informative specify inshore-offshore gradient or similar As all of our sites were open-ocean with the transect running offshore we have changed this to "along a 550km offshore transect". The full details of which are now clearly described in the legend and map in figure 1.

21: strong 45N2O signature makes no sense without explanation of the methods
Agreed and have inserted 15 NO 2 higher up in the abstract but a full explanation is not possible with just 150 words. Line 19.
46: here and in many other places the authors use quotation marks in an unclear manner -does this indicate dubious results or what?
Removed as there use was a bit arbitrary on rereading the document.

64: Thaumarchaeota is used elsewhere and should be correct
Corrected to Thaumarchaea throughout.

87: unclear sentence -how can the MLD extend to 25 m and then increase steadily?
Corrected and now reads "the mixed layer depth (MLD) extended down to approximately 20m to 25m and then density increased steadily to a sharp inflection at 35m to 40m, marking the base of the pycnocline (Fig. 1b)." Lines 88-90. 92: what is "the true anoxic core"?? This is a thorny issue but we have now gone with "the functionally anoxic core of the OMZ 3 " where the reference cited explains in detail that, although there may still be a handful of nano-molar amounts of oxygen (Thamdrup pers. comm), oxygen is, for all intents and purposes, functionally unavailable to aerobes and the core is therefore functionally anoxic. This has no real bearing on our overall story and it is a passing line in the opening results describing the broader water column in the OMZ. Lines 94-96. 93: unclear: nitrite and N2O minima were found at 350 m and occurred at 400-450 m??
The text has been edited to clarify this point "Deeper, at around 350m, oxygen became comparatively constant, with the functionally anoxic core of the OMZ 3 , where both the secondary nitrite maxima and N 2 O minima were measured, occurring deeper still at 400m to 450m (Fig. S1a). lines 94-96. Fig. S2 is very difficult to understand. Why are the same data points shown in multiple frames in both a and b? Why do the sections overlap sometimes but not always?
The co-plot function in R can be used to represent multivariate data but its usage might not be that familiar to everyone. Below are all the available datasets from transects giving the best coverage closest to ours in the tropical Pacific -we are MT in maroon, vertical -92.5W. Fig. S2 tries to show our profiles relative to all other profiles when the data are either sampled according to latitude or longitude. The programme also tries to sample or bin the data evenlythough the data are clearly not evenly distributed (e.g. between -100 to -130E). I have now reduced the overlap as much as possible but it is unavoidable in the longitude orientation because transect 130 and 8 slice through our transect from NW to SE and the bin, sampling either side of -100E, picks up our transect at 92.5W twice. Hope it is clearer now.
107: is there such a thing as O2-free nitrogen gas? (and OFM is used but not defined anywhere) No, in reality there probably isn't but oxygen-free-nitrogen (OFN) is just a common trade name of a routine gas. Changed to nitrogen on line 114 and the purity of our "OFN" is now defined in Table 1 where we provide a summary of our treatments.
120: exponential increase is confusing without stating the direction of oxygen concentrations -it is an exponential decrease with increasing oxygen We have modified the statement to "The overall exponential increase in production of N 2 O with oxygen decreasing below 30 µmol O 2 L -1 is not only consistent with N 2 O accumulating below 30 µmol O 2 L -1 in the water column (Fig. 1d) but also with distributions seen in many parts of the tropical North Pacific (as above, Fig. S2)." We have also edited this clause throughout the text to include decreasing. For example lines 18-19 "to decreasing oxygen between 1-30µmol O 2 L -1 within and below the oxycline" and 129-130 and all others. 121: it is not obvious to me that the exponential function is consistent with the in situ distribution The exponential response that we measure in a bottle is a pure biological response to decreasing oxygen, whereas the profile is an integral of both that biology and abiotic, physical factors. Both biology and physics shape the profile and that is what we capture, very well, with our 1D model (See new version in Fig. 5). The model is parameterized (M2, Table 2) to generate N 2 O as a single biological response to decreasing oxygen which physics then distributes, shapes, to a steady-state profile in the water column. For example, diffusion through the pycnocline is slow, hence the accumulation of N 2 O at the base of the pycnocline. As an OMZ is a consequence of rapid biology respiring oxygen and sluggish physics failing to replenish that oxygen -oxygen is slow in, N 2 O (and CO 2 ) is slow out etc.
124: these developments are by no means "approximately linear". Two out of four clearly cease completely after 12 h, and the two others clearly decelerate after 20 h -the effect seems to be depth dependent. The underestimation of rates in the long incubations adds further uncertainty to issue #1 above.
See point 9 for reviewer 1. The last point is answered as part of the rebuttal to main point of criticism from reviewer 3 above i.e. we are not largely underestimating N 2 O production.
200-2: please explain -why does the fact that nitrification is active lead the authors to expect no N2O production from nitrite? Nitrifier denitrification depends on nitrification.
With all due respect the reviewer is citing this phrase out of context. The paragraph started by setting the scene on the previous line with "The overwhelming majority of studies have argued for nitrification by ammonia oxidizing bacteria (AOB) ( 15 NH 4 + → 15 NH 2 OH→ ( 15 NO + 15 N 2 O) → 15 NO 2 -) as the principal source of oceanic N 2 O 4,5 ) but this view is being revised 6 . The potential for nitrification is clearly evident in our data and, that being so, then we would not expect any 15 N-N 2 O production at all with 15 N-NO 2 as the substrate." As for reviewer 2, point 4, this section has been edited and the material is now covered elsewhere. 225-6: the authors did not measure net nitrification (i.e. increase in concentrations of nitrite+nitrate), I believe. Furthermore, Kalvelage and coworkers have reported nitrate reduction to 20 µM oxygen in OMZ waters, so why would 1 µM exclude the process? The potential for nitrate being the source of 14N in N2O should be discussed further.
An oversight by the reviewer perhaps as we did measure net nitrification; as was stated in the methods, results and the legend for

240-1: this is pure speculation -being better adapted doesn't mean being perfect
We did not mean to imply perfect, and don't think that we do. This is one line of inference at the end of the proceeding argument. The point is to emphasize the need to recognize a major route of N 2 O production as a real niche rather than as a consequence of simple oxygen stress (which drives N 2 O production in AOB) and we would prefer to keep it in. It now appears on lines 254-257. 281-2: air-sea exchange rates should be independent of the assumptions about pathways of N2O production?
We agree with the reviewer that air-sea exchange rates should be independent of the assumptions about pathways of N 2 O production. Nevertheless, air-sea exchange depends on the air-sea concentration gradient, so if the model over/under estimated N 2 O production (regardless of the pathway) then the air-sea exchange may also be erroneous. Here our model agrees very well with our observations (Fig. 5)  We have added the respective definitions. We do, however, disagree with the reviewers' request for different markers on panels a, and b. The whole point of our approach is to not worry about the idiosyncrasies of the individual sites or profiles but rather to present an analysis of the entire dataset. Adding colour or symbols to a, and b, just adds noise and we feel that this would not be useful. Pooling the data for treatments 3+4 and 5+6 changes the overall distribution of the data as we are, in effect, doubling the sample size from 12 to 24 in each case and that affects what is classed as an outlier in the box-plots. Since recalculating, to express our data as total N 2 O production, in line with the reviewer, the overall distributions of the data in the boxplots have changed ever so slightly, the effect of treatment is now even stronger (e.g. Likelihood ratio test for treatment is compared to 30.29) but our model output and conclusions remain the same.   The authors have done a thorough and commendable job of addressing my concerns in the prior review, notably regarding the disconnect in the qPCR counts and clarifying the overall presentation of the experimental/sampling design and bottle effects. This is a solid experimental study on a potentially substantial, and somewhat overlooked, pathway to OMZ greenhouse gas production. There are many mechanistic details about this process that remain to be fleshed out. I suspect this paper will be a powerful motivator for such work.
Reviewer #3 (Remarks to the Author): The authors have revised the paper extensively and have resolved many issues. My most serious concern remains, however, namely that the reported 15N-N2O production rates greatly underestimate total N2O production. This might in part to be due to a couple of mistakes in my original comments for which I apologize. Although the error is not as large as I thought originally, I maintain that it might undermine the central conclusions.
Authors' comments: "We think there's just been a simple mistake here. The reviewer begins by stating that "Based on the relative accumulation of masses 45 and 46 (Fig. 2c) . This tells us that the vast majority of N2O cannot be due to denitrification because the measured frequency of 45N2O is far above that predicted for denitrification given the 15N labelling of the NO2-pool (>86%). If N2O were being produced solely through denitrification then, with random isotope pairing, the labelling of the N2O would be binomially distributed relative to frequency of 14N to 15N in the NO2-pool and we would get 45N2O produced along the 1:1 line in Fig. 2c -which we do not. So it seems to us that the premise of the argument is not correct." I made two mistakes in my original comment, which might have confused the authors, but the premise of my argument that "The reported 15N-N2O production rates greatly underestimate total N2O production" still holds, and the same applies to the newly calculated total N2O production rates.
Regarding my mistakes: (1) While Fig. 2c did not show 46N2O production directly, it did so indirectly because the ordinate, 45N2O predicted for denitrification, is directly related to 46N2O production (Equation 1, l. 368). My estimate of the production ratio of 45N2O to 46N2O of 50:1 was wrong, however. If I understand l. 115 correctly (that 81% refers to the contribution of 45N2O to 15N-N2O; it can't refer to the relative increase above the expected value although that is what the text seems to imply -I didn't get this the 1st time), this ratio was on average 4:1 (0.81/(1-0.81)).
(2) Because the authors write in the discussion that "Put simply, the majority of N in the N2O produced was actually 14N that was not derived from our 15N-NO2-tracer", I assumed that the authors agreed with me in the principles of isotope pairing that apply to N2O formed through nitrifier-denitrification. I understand now that they don't and will therefore explain this issue in more detail: Press) with the two steps being analogous to those found in canonical denitrifiers. The process is well-described in AOB. The authors argue that N2O production in AOA occurs through a similar, if not identical pathway, which is agreement with the most recent literature. It is possible that NO is a free intermediate in ammonium oxidation in AOA, such that the mixing of N atoms originating from ammonium and nitrite, respectively occurs in the NO pool rather than (or as well as) in the nitrite pool (NH4+ => NO; NO2-=> NO; 2NO => N2O). Regardless, the step leading to N2O formation is NO reduction, as is the case in canonical and AOB nitrifier denitrification. This has important implications for the calculations of total N2O production based on 15N-nitrite incubations as in the present case.
If N2O forms from either nitrite or NO reduction, the nitrogen isotope composition of N2O is the result of random isotope pairing during the reduction of 2NO to N2O. This means that N2O of masses 44, 45, and 46 will form at a ratio of (1-FNO)^2 : 2*FNO*(1-FNO) : FNO^2, where FNO represents the mol fraction of 15N in the NO pool. This further implies that even if FNO is not known, the total production of N2O (masses 44 + 45 + 46) can be determined from the production of 45N2O and 46N2O as described by Nielsen (FEMS Ecol 86:357-62, 1992). This is the basis of Nielsen's well-established isotope pairing technique, which is widely used to determine denitrification rates in intact sediment cores. As I pointed out in my original comment, the situation in the sediment incubations is analogous to that in the present study: 15N-nitrate is added to the water column and reduced to N2O (and ultimately N2) in the sediment, and at some point during the process, the stream of "exogenous" 15N is diluted by 14N originating from nitrification. In fact, the 1st author has developed an elegant technique to determine both denitrification and anammox in sediment cores based on this principle.
Based on all this, I am very surprised that the authors in their new calculations of total N2O production have chosen to treat nitrifier-denitrification as an anammox-type process (l. 375-383). Anammox is characterized by 1:1 (rather than random) pairing of N atoms originating from nitrite and ammonium, respectively. This pairing is brought about by the 1:1 reaction of NO and NH4+ to form hydrazine (N2H4), which is unique to the highly specialized anammox bacteria. Anammox bacteria do not produce N2O (it seems) and the authors provide no justification whatsoever for assuming the involvement of a similar, asymmetrical process in nitrifier denitrification. All available knowledge points to random isotope pairing.
Thus, the authors should either argue convincingly for a new pathway of N2O formation with a unique 1:1 isotope pairing, which is what they have based their present calculations on, or recalculate their total N2O production rates assuming the more realistic random isotope pairing expected for nitrifier denitrification. For a production ratio of 45N2O to 46N2O of 4:1 (as estimated above) the total rate will be about twice the rate of 45N2O production. This change is not as serious as I had anticipated in my original comments, but it is still substantial, and, as mentioned in my original comment, the ratio of 45N2O to 46N2O production seems to be highly variable, and recalculation will therefore not simply scale up the rates proportionally. Thus, I strongly disagree with the authors' statement: "Please also note -that neither of the two concerns raised by the reviewer here would have any effect on either our revised or original story. We experimentally manipulated oxygen and directly measured an exponential increase in 15N-N2O. The residual variation that couldn't be explained by oxygen correlates with archaeal gene abundance. Also, parameterizing a 1D model with our nonlinear model coefficients reproduces the pattern of N2O in the ocean (incredibly well!) and, with that model, we can balance direct estimates of air sea exchange -the issues raised by this reviewer do not change any of that." l263-4: I am lost here. According to Koslowski, hybrid N2O formation could be a spontaneous process, and there is no indication of a link to energy conservation. The sentence refers to ref. 36 on AOB Nitrosomonas, which uses a different pathway, and there is no evidence of energy conservation from N2O formation in fungi, as far as I know.
Having now read this again we can see where the confusion lay and have edited the text accordingly and removed any reference to fungi. The current point of view is that the archaea may use some hybrid mechanism to produce N 2 O which, if spontaneous, wouldn't itself be linked to energy conservation but we can argue that the production of the likely precursor substrates NH 2 OH and NO would. We have edited the text to clarify and tone down our claim on lines 282-285.
The overall argument may, however, not be that straightforward. For example, we simply measured an exponential increase in N 2 O production as a function of declining oxygen and then, Nitrate reduction (nmol L d-1) Oxygen ( Thanks for spotting this: oxyen is now oxygen. A general note: The paper now refers to the Thaumarchaeotal N2O pathway as similar to codenitrification. I would recommend using the term hybrid N2O formation (at least in the abstract and introduction), which is used by Kozlowski and seems to be catching on rapidly at conferences.
We have adopted hybrid N 2 O formation throughout and included further discussion of the potential routes of N 2 O production in the Methods in line with this and the comments above. See new lines 26, 79, 283, 292, 333, 337, 404 and 424.