the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 17 Nov 2022
Process Rate Estimator: A novel model to predict total denitrification using natural abundance stable isotopes of N2O
Abstract. Total denitrification, the natural process capable of removing reactive N from ecosystems through conversion to N2, is one of the most poorly constrained processes in terrestrial N cycling. In situ quantification of total denitrification could help identify mitigation options for N pollution. This study provides proof-of-concept for a novel natural abundance isotope based model for depth differentiated in situ quantification of total denitrification; it does so by examining the use-case of the impact of wheat (Triticum aestivum) varieties with different root biomass on total denitrification. We set up a mesocosm experiment in 1.5 m tall lysimeters with four wheat varieties, each replicated three times. Temporal data for soil moisture, nitrous oxide (N2O) concentrations in the soil pore space, site preference (SP) and δ18O values of soil pore space N2O were collected at soil depths of 7.5, 30, 60, 90 and 120 cm over a five month growing period and used as input variables in the new model. Here, we define total denitrification as gross N2O consumption, with N2O produced either through nitrification or denitrification. The model, further referred to as ‘Process Rate Estimator’ or PRE, constrains temporally explicit gross N2O production and consumption rates at each depth increment based on a combination of diffusion and isotope mixing and fractionation models. Estimated production and consumption of N2O, integrated over the five month experiment, ranged from 3.9 to 170.3 kg N ha-1, with a trend for greater N2O production from denitrification compared to nitrification. N2O concentrations where greatest at 60 and 90 cm depth, while N2O production and consumption peaked at 7.5 and 30 cm depth, illustrating the important role of N2O dynamics along the soil profile in understanding ecosystem N budgets. Both N2O production and consumption were greater in varieties that had previously been characterized to have greater root biomass. We demonstrate that PRE is able to constrain nitrification and denitrification leading to gross daily N2O production, and gross reduction to N2 across the depth profile, based on the temporal change in concentrations, δ18O and SP of N2O. We conclude that our results support the potential of PRE to estimate total denitrification in situ, which could form the basis for developing promising strategies to reduce N pollution.
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RC1: 'Comment on bg-2022-221', Anonymous Referee #1, 23 Dec 2022
Dear authors, dear editors
General comments:
This is an interesting and important paper on soil N2O dynamics, including detailed insight into its production and consumption processes along the soil profile. Although the method presented relies on multiple assumptions I think this is a very interesting approach allowing for a better understanding of N2O origins and sinks. I mostly wonder if this approach can be transferred to the real field conditions. Since you used sieved and homogenized soil, the diffusion can be easily fitted and you do not deal with inhomogeneity issues. For example, by intact soil profiles, you would need to have individual values regarding density, moisture, or d18O of soil water for each layer. This experiment was carried out in a greenhouse, how would wind impact your modelling procedure? A discussion on the possible perspective of transferring this method to the field would be a valuable issue in your manuscript, so I would suggest adding this.
I have also some doubts about the calculations. In the appendix you made some simplifications of the equations which are not justified and difficult to follow. Please expand your explanations, in below specific comments I have indicated what exactly I’ve found unclear.
Specific comments:
Please use delta symbols in your manuscript.
L79 – Recently published method for applying 15N tracer in field in N2-depleted atmosphere should be mentioned here (Well et al., 2019, RCM 33: 437-448). This is a compromise overcoming difficulties associated with 15N tracing (lower 15N levels can be applied, better sensitivity in N2-depleted atmosphere) and N2-free atmosphere experiments (it can be applied in field conditions!)
L83 – Also for natural abundance N2O analyses an important progress has been achieved recently, Lewicka-Szczebak et al., 2020 (BG 17 (22): 5513-5537) proposed a modelling approach based on all 3 isotopic signatures of N2O. It was validated for field conditions application and can provide quantification of N2O reduction also providing uncertainity assessment.
L250 tests were included
L269 you need to define how eta values are defined and which values you applied for them
Table 1 – there is new review paper by Yu et al, 2020 (RCM 34 (20): e8858, appendix) summarising the values, it would be most up to date to cite these (there are some important changes in the ranges)
L 286 you say that there is a common range for nitrification and fungal denitrification – in the most recent review (Yu et al., 2020) it has been shown that the d18O for nitrification should be slightly different than assumed in previous publications, you should either decide which of these processes is more relevant for your study or assume a slightly wider range for d18O
Eq 7,8 – eta*F reduced/diffused – you make open system assumption in your equations – definitely right for diffusion, but can be doubt for N2O reduction, there might be values which cannot be explained with open system equation (Lewicka-Szczebak et al., 2014, 2017), or you can wrongly attribute this to larger proportion of nitrification. Especially given that you have large reduction it makes big difference if using open or closed system equations. I would check what is the difference and report this. You have only justified using the open system equation with the argument of simplified maths, but I think this generates significant bias. The requirement for using open system equation is the equilibrium of the fluxes in and out (Fry, 2006) and you clearly do not have this between N2O production and reduction.
Did you take into account atmospheric N2O diffusing into the soil? Have you sampled ambient air for N2O isotopic analyses?
L 555 (Appendix) – “With various terms cancelling out, the equation can be rewritten as:” – why can you cancel out “various things”, what are these “various things” and how this cancelling out influences the final result?
L563 (Appendix) – “For ât approaching 0, the equation can be further simplified as:” – why can you assume Dt approaching 0? It is one day, right? When you are using fluxes in your equations you need the time factor to be included in the equations, I guess. What are the units for the fluxes used in your Eq 7 and 8?
Table 3 You have given the N2O fluxes without time units. For which time period are the amounts given (per hour, per day?)
Table 5 – same as above
L355-357 – I am not sure if Fig 1 really supports this statement. For some isotopic signatures you have really large variations within the 2 weeks time, eg. SP values 7.5cm depth
L361 – very low SP – cannot be explained with any known literature data?! Can this be due to some measurement or evaluation problem? As these are individual samples you should carefully look on their measurements – was the N2O concentration in good range? Check your normalisation procedure for evaluation of SP data. What is your lowest SP standard? If your lowest standard value is near atmospheric air (eg. +18) then your normalisation for such low values may produce large offset (see Mohn et al, 2014).
You also have d15N data, why not using them in the modelling as well? Maybe then can be useful in distinguishing further processes like nitrification and fungal denitrification (in case you would also analyse the substrates).
Fig 3b, 3c – why there are no error bars for the points before day20 and after day100?
Section 2 – have you analysed d18O of soil water? If so, please describe, which method, how many samples etc. If not, please justify your assumption on -9.9 permil.
Citation: https://doi.org/10.5194/bg-2022-221-RC1 -
AC1: 'Reply on RC1', Charlotte Decock, 14 Mar 2023
We thank the reviewers for their constructive and thorough comments. Please find reviewer comments followed by author response to each column below. Author responses are shown in bold.
Dear authors, dear editors
General comments:
This is an interesting and important paper on soil N2O dynamics, including detailed insight into its production and consumption processes along the soil profile. Although the method presented relies on multiple assumptions I think this is a very interesting approach allowing for a better understanding of N2O origins and sinks. I mostly wonder if this approach can be transferred to the real field conditions. Since you used sieved and homogenized soil, the diffusion can be easily fitted and you do not deal with inhomogeneity issues. For example, by intact soil profiles, you would need to have individual values regarding density, moisture, or δ18O of soil water for each layer. This experiment was carried out in a greenhouse, how would wind impact your modelling procedure? A discussion on the possible perspective of transferring this method to the field would be a valuable issue in your manuscript, so I would suggest adding this. I have also some doubts about the calculations. In the appendix you made some simplifications of the equations which are not justified and difficult to follow. Please expand your explanations, in below specific comments I have indicated what exactly I’ve found unclear.
We greatly appreciate the reviewer’s positive evaluation of the importance of our work and the constructive comments and suggestions to further improve our modeling approach. The paper we present is a proof-of-concept study. To the greatest extent possible, we will integrate suggestions and recommendations in the revised manuscript. Nevertheless, we found some suggestions and comments are beyond the scope of this study, and present great opportunities for future research and development. Details are outlined below.
We acknowledge the reviewer’s concern about transferability of the modeling approach to a field situation and will include text in the discussion section addressing important considerations for field applications. Any previous research on limitations of diffusion models in a field setting would apply to this study as well, but are beyond the scope of this work. We appreciate the reviewer’s suggestion of recommending depth differentiated measurements of bulk density, soil moisture, and δ18O of soil water. The current model already includes depth and time differentiated values for soil moisture based on in-situ measurements. Bulk density was not significantly different between depth increments in our experiment. Adding depth differentiated bulk density and δ18O of soil water can easily be done in future projects.
As to the question of how wind would impact the modeling outcomes, we can only speculate. We acknowledge that wind causes pressure differences at the soil surface which will affect the flux. However, one can argue how well impacts of wind are captured in published N2O flux data from field trials. When fluxes are measured using static flux chambers, the surface in the chamber will be sheltered from the wind by the chamber and wind effects may be missed. Studies that compare N2O surface fluxes measured using static flux chambers with N2O flux estimated based on the diffusion gradient method consistently see discrepancies between the two methods. Flux measurements using static flux chambers often show hot moments, characterized by brief but sharp pulses in N2O emissions. The gradient method does not commonly show equally sharp pulses in N2O concentrations in the subsurface, thereby failing to predict the surface to atmosphere N2O flux accurately. We believe that surface and subsurface N2O dynamics may be decoupled, and that the hot moments often observed in surface fluxes may be produced in the top few cm of soil, above the point where the shallowest diffusion sampler may be installed. Given that our method primarily aims to estimate total denitrification throughout the profile based on N2O concentrations and isotope values in that profile, combined with many observations in the literature that suggest at least a partial decoupling of surface and subsurface N2O dynamics, we would expect the impact of wind on our estimates of total denitrification in the soil profile to be relatively low.
Based on detailed comments of the reviewer on the proof for the equations used in the model, we will add a more detailed description in the appendix of the revised manuscript where the proof is delineated.
Specific comments:
Please use delta symbols in your manuscript.
We assume that the reviewer is referring to delta symbols for shown isotope values. We tried to refer to all isotope values with delta symbols but will check the manuscript again thoroughly if this was accidently not done.
L79 – Recently published method for applying 15N tracer in field in N2-depleted atmosphere should be mentioned here (Well et al., 2019, RCM 33: 437-448). This is a compromise overcoming difficulties associated with 15N tracing (lower 15N levels can be applied, better sensitivity in N2-depleted atmosphere) and N2-free atmosphere experiments (it can be applied in field conditions!)
We will acknowledge the newly proposed method in the revised manuscript.
L83 – Also for natural abundance N2O analyses an important progress has been achieved recently, Lewicka-Szczebak et al., 2020 (BG 17 (22): 5513-5537) proposed a modelling approach based on all 3 isotopic signatures of N2O. It was validated for field conditions application and can provide quantification of N2O reduction also providing uncertainity assessment.
We appreciate reference to this study. We will suggest including the 3 isotopes of N2O for future developments of the model in the revised manuscript.
L250 tests were included
Thank you, we will fix this grammatical error.
L269 you need to define how eta values are defined and which values you applied for them Table 1 – there is new review paper by Yu et al, 2020 (RCM 34 (20): e8858, appendix) summarising the values, it would be most up to date to cite these (there are some important changes in the ranges)
We will rerun the analyses with the newest end members and eta values summarized in Yu et al. 2020 and include appropriate definitions in the revised manuscript. We do not expect the model outcomes to change drastically, based on our evaluation of the impact of uncertainty around the isotope endmembers on model predictions.
L 286 you say that there is a common range for nitrification and fungal denitrification – in the most recent review (Yu et al., 2020) it has been shown that the d18O for nitrification should be slightly different than assumed in previous publications, you should either decide which of these processes is more relevant for your study or assume a slightly wider range for d18O
Thank you for the suggestion, we will change the revised manuscript accordingly.
Eq 7,8 – eta*F reduced/diffused – you make open system assumption in your equations – definitely right for diffusion, but can be doubt for N2O reduction, there might be values which cannot be explained with open system equation (Lewicka-Szczebak et al., 2014, 2017), or you can wrongly attribute this to larger proportion of nitrification. Especially given that you have large reduction it makes big difference if using open or closed system equations. I would check what is the difference and report this. You have only justified using the open system equation with the argument of simplified maths, but I think this generates significant bias. The requirement for using open system equation is the equilibrium of the fluxes in and out (Fry, 2006) and you clearly do not have this between N2O production and reduction.
We acknowledge that carefully considering open versus closed system dynamics is important. If N2O production and reduction occur simultaneously, both open or closed dynamics could occur. The reviewer refers to the requirement of equilibrium between the fluxes in and out for open system dynamics, and argues this is not the case in our study. We kindly disagree with this assessment. Given the slow but steady change of N2O and isotope values over time observed in our study, fluxes in and out may well be at near equilibrium in distinct time points. In the study by Lewicka-Szczebak and collegues (2017), instantaneous N2O emitted from the soil surface was measured during an incubation, where a N2O pulse was observed following application of fertilizer N. When plotting isotope values of N2O in function of the residual N2O fraction, a logarithmic fit was found, which could be described by the Rayleigh equation that describes N2O fractionation under closed system dynamics. This clearly illustrates that in their study, closed system dynamics prevailed during N2O reduction. It should be noted, however, that the patterns observed in Lewicka-Szczebak et al. (2017) are only expected to occur if N2O source processes remain constant, while there is a progressive reduction of N2O over time. If N2O production from nitrification increase or decrease over time, very different patterns would have emerged. The figures below show simulated relationships between SP of the instantaneous product and the residual substrate fraction under scenarios where N2O production is constant over time, vs. where N2O production from nitrification and denitrification changes over time, for open vs. closed system dynamics. In all scenarios, we assumed that the residual fraction of N2O decreases progressively over time (see figure in attached supplement).
We argue that, while the study by Lewicka-Szczebak et al. (2017) marked an important milestone in furthering how to interpret N2O isotope values, the study does not provide unequivocal evidence that closed system dynamics will prevail in all scenarios where N2O production and reduction occur simultaneously. This leaves the question, when is it appropriate to use open vs. closed system dynamics? In a simulation by Denk et al. 2017, it was shown that the difference between open and closed system dynamics becomes small at small time steps, even when the fraction of residual substrate becomes very small. Given that closed system dynamics would lead to a system of complex non-linear equations that are much harder to solve numerically, we opted to use open system dynamics and a small time step. We will elaborate on this point in the discussion, including recommendations for future research to provide more clarity on this issue.
Denk, T. R. A., et al. (2017). "The nitrogen cycle: A review of isotope effects and isotope modeling approaches." Soil Biology & Biochemistry 105: 121-137. (Fig. 7)
Did you take into account atmospheric N2O diffusing into the soil? Have you sampled ambient air for N2O isotopic analyses?
Ambient air samples were taken and analyzed for N2O concentrations as well as isotope values of N2O. The model does calculate diffusion between the ambient air and the 0-7 cm depth increment. A positive value would indicate a net flux out of the soil, a negative value a net flux into the soil.
L 555 (Appendix) – “With various terms cancelling out, the equation can be rewritten as:” – why can you cancel out “various things”, what are these “various things” and how this cancelling out influences the final result?
Please see answer in attached document. We were not able to insert equations in the easily in the comment post box.
L563 (Appendix) – “For approaching 0, the equation can be further simplified as:” – why can you assume Dt approaching 0? It is one day, right? When you are using fluxes in your equations you need the time factor to be included in the equations, I guess. What are the units for the fluxes used in your Eq 7 and 8?
Please see answer in attached document. We were not able to insert equations in the easily in the comment post box.
Table 3 You have given the N2O fluxes without time units. For which time period are the amounts given (per hour, per day?) Table 5 – same as above
The values are cumulative N2O production and consumption rates over the experimental period, which was approximately 5 months. We will add this information in the table captions.
L355-357 – I am not sure if Fig 1 really supports this statement. For some isotopic signatures you have really large variations within the 2 weeks time, eg. SP values 7.5cm depth
The reviewer refers to the statement “Similarly, subsurface isotope values of N2O showed a relatively consistent temporal pattern (Fig. 1). The temporal patterns in subsurface N2O concentrations and isotope concentrations observed in this and other studies (van Groenigen 2005, Verhoeven 2019) suggest that a sampling frequency of once every two weeks or once a month may be sufficient to adequately capture subsurface N2O dynamics.” While we agree with the reviewer that some of the variation in isotope values between sampling points is relatively high, we argue that there is a clear and strong pattern of increasing isotope values over the course of the experimental period, that appears stronger than the variations between reps and sampling points that are closer together in time (See Fig. 1).
L361 – very low SP – cannot be explained with any known literature data?! Can this be due to some measurement or evaluation problem? As these are individual samples you should carefully look on their measurements – was the N2O concentration in good range? Check your normalisation procedure for evaluation of SP data. What is your lowest SP standard? If your lowest standard value is near atmospheric air (eg. +18) then your normalisation for such low values may produce large offset (see Mohn et al, 2014).
IRMS calibration was done with two isotopically different standards (see Verhoeven 2019). We did not omit any data which had passed our internal quality check. However, a small fraction of the samples was analyzed before we implemented an activated charcoal trap. This trap was implemented in our inlet system as we observed strong mass interferences from unknown sources. We speculate that especially soil pore gas samples can potentially be contaminated with VOCs or other gaseous compounds interfering with the measurement. The very low SP values stem from the period when measuring without an activated charcoal trap. N2O concentrations were generally in a good range. Our lowest SP standard is at -1.62 permil.
You also have d15N data, why not using them in the modelling as well? Maybe then can be useful in distinguishing further processes like nitrification and fungal denitrification (in case you would also analyse the substrates).
We appreciate the reviewer’s suggestion. Values of δ15N-N2O are impacted by the δ15N of the substrate, which can change rapidly and strongly over time (Decock and Six, 2013). In the absence of data on δ15N of the substrate, we did not feel confident including δ15N as a constraint. However, expanding the model to include δ15N data may be a great opportunity for future developments.
Fig 3b, 3c – why there are no error bars for the points before day20 and after day100?
The error bars are so small that they can’t be seen on the figure.
Section 2 – have you analysed d18O of soil water? If so, please describe, which method, how many samples etc. If not, please justify your assumption on -9.9 permil.
The δ18O value measured for tapwater at the facility was used in this study. The value is actually -11 permil. We accidentally copied the wrong value over from Verhoeven et al. 2019 in the footnote under table 1. We will correct this in the revised manuscript and add details on the method to measure δ18O in tapwater in the materials and methods section. We will also elaborate in the discussion on how time and depth differentiated measurements of soil water δ18O are recommended for field studies.
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AC1: 'Reply on RC1', Charlotte Decock, 14 Mar 2023
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CC1: 'Comment on bg-2022-221', Reinhard Well, 05 Jan 2023
Comment by Reinhard Well, Thuenen-Institute, Braunschweig, Germany
The attempt to use soil air N2O isotopes to constrain N2O processes is timely in view of many data reports lacking conceptual or physical models to interpret results. Therefore the presented approach is really needed and very promising from my view. In view of the close deadline of open discussion I could not find time to look at this interesting paper in detail, unfortunately, but just went briefly through methods and key results. I am impressed by the very nice lysimeter study yielding a very valuable data-set as far as I can see.
With regard to interpretation and calculations I came across the following points that might be subject to further consideration:
- The magnitude of calculated denitrification rates of up to > 100 kg N/ha in about 5 month is quite high for terrestrial mineral soils. I would not say impossible but quite astonishing. Total N2o fluxes are, however, in typical range, giving N2O/(N2O+N2) ratios about 1-2%, eg much lower compared to most previous reports. Still not impossible, but astonishing, maybe due to high pH and/or low diffusivity? The estimated N2O production from nitrification (N2Onit), however, is impossible from my view. It is well known that the N2O yield of nitrification is always very small with values around 0.1% typical and rarely above 1% (e.g. Hink, L., et al. (2017). "Archaea produce lower yields of N2O than bacteria during aerobic ammonia oxidation in soil." Environmental Microbiology 19(12): 4829-4837. But you report N2Onit up to 25 kg/5 month. Assuming a very high N2O yield of nitrification of 1% this would mean gross nitrification was 2500 kg N/ha/5 month. I think this is far beyond all previous reports in soils.
- What could be the reason for possible overestimating N2O production and consumption? I think it could be the fact that you assume open system dynamics for isotopic fractionation during N2o reduction. I recall we had a discussion on this after the Decock & Six review in 2013 and my impression was that later on most authors assumed that closed system dynamics are more probable for soil denitrification. In the study of Lewicka-Szczebak, D., et al. (2017). "Quantifying N2O reduction to N2 based on N2O isotopocules – validation with independent methods (helium incubation and 15N gas flux method)." Biogeosciences 14(3): 711-732. this could be confirmed by independent measurement of N2 fluxes, since a match of NA isotopes and 15N-tracing was only obtained when assuming closed system dynamics. To illustrate the huge difference in calculated N2O reduction when using closed or open system dynamics one might use the equations for closed and open system fractionation shown in in Decock and Six 2013 and calculate SP using the unreduced fraction of N2O (f) of e.g 0.02 according to Monte Calme treatment in Table 5, giving for open system: SP = SP0 - εSP (1 - f) = -2.4permil - (-5.3permil) * (1-0.02) = 2.8 per mil; for closed system: SP = SP0 + εSP * ln(f) = -2.4permil + (-5.3permil) * ln(0.02) = 18.3 permil. So this shows the huge difference of both approaches for small f values, while results are more similar for f values close to 1. Looking at the SP value of open system dynamics yielding f = 0.02 we can check which f value would be obtained by closed system dynamics if we solve the equation for f giving: f = exp((SP-SP0)/eSP) = 0.38. This shows that closed system would lead to much higher N2O/(N2+N2O ) ratios.
- Strong overestimation of N2O reduction due to open system assumption would also explain the very high N2Onit values: if the combination of SP and d18O values yields a fraction from nitrification of say 30%, then with the large values of total N2O consumption you end up with these high numbers for N2Onit. So possibly, by assuming closed system dynamics you would solve this contradiction.
- Some more detailed discussion how N2O consumption could be larger than production would be helpful.
- I was astonished about another number: bulk density of > 1.7 after sieving and packing. How in the world did you achieve this with sieved loamy soil? I think it is only possible with extreme compaction and I wonder how wheat could grow. If you used indeed extreme compaction procedure then you might report why you chose this and how it was achieved. With BD about 1.7, diffusivity must have been extremely low during moist phases and thus could indeed explain extreme denitrification rates. I think the paper would gain if you discussed the uncertainty from calculated diffusivity and assuming constant BD. You might also consider that for low air filled porosity (as maybe in your case ) there are special equations for Ds (eg Sallam, A., et al. (1984). "Measurement of Gas Diffusion Coefficient under Relatively Low Air-filled Porosity." Soil Science Society of America Journal 48(1): 3-6)
But irrespective of the question whether my concerns are justified or not, I think your approach is really promising. Would be nice if someone would check its outcome using independent methods soon. I always found this very helpful when evaluating new denitrification methods.
Citation: https://doi.org/10.5194/bg-2022-221-CC1 -
AC2: 'Reply on CC1', Charlotte Decock, 14 Mar 2023
We thank the reviewers for their constructive and thorough comments. Please find reviewer comments followed by author response to each column below. Author responses are shown in bold.
Comment by Reinhard Well, Thuenen-Institute, Braunschweig, Germany
The attempt to use soil air N2O isotopes to constrain N2O processes is timely in view of many data reports lacking conceptual or physical models to interpret results. Therefore the presented approach is really needed and very promising from my view. In view of the close deadline of open discussion I could not find time to look at this interesting paper in detail, unfortunately, but just went briefly through methods and key results. I am impressed by the very nice lysimeter study yielding a very valuable data-set as far as I can see.
We thank the reviewer for this kind and encouraging evaluation of our work.
With regard to interpretation and calculations I came across the following points that might be subject to further consideration:
The magnitude of calculated denitrification rates of up to > 100 kg N/ha in about 5 month is quite high for terrestrial mineral soils. I would not say impossible but quite astonishing. Total N2o fluxes are, however, in typical range, giving N2O/(N2O+N2) ratios about 1-2%, eg much lower compared to most previous reports. Still not impossible, but astonishing, maybe due to high pH and/or low diffusivity?
We agree with the reviewer that total denitrification rates are high but within range of what has been observed in the literature. We provide an extensive discussion on potential explanations in the manuscript, including limitations of alternative methods to estimate total denitrification.
The estimated N2O production from nitrification (N2Onit), however, is impossible from my view. It is well known that the N2O yield of nitrification is always very small with values around 0.1% typical and rarely above 1% (e.g. Hink, L., et al. (2017). "Archaea produce lower yields of N2O than bacteria during aerobic ammonia oxidation in soil."Environmental Microbiology 19(12): 4829-4837. But you report N2Onit up to 25 kg/5 month. Assuming a very high N2O yield of nitrification of 1% this would mean gross nitrification was 2500 kg N/ha/5 month. I think this is far beyond all previous reports in soils.
We appreciate the back-of-the envelope calculations provided here and feel it is a great way to evaluate if the rate constraints by our model are realistic or not. We do not think, however, that a gross nitrification rate of 2500 kg N/ha/5 months is unrealistic. Gross nitrification rates in agricultural soil have been found to range between 0.2 and 10 mg N kg soil-1 day-1(Booth et al., 2005). Assuming a rate of 5 mg N kg soil-1 day-1 and 2,000,000 kg soil in a 15 cm depth increment, this would come down to 1500 kg N ha-1 over 150 days. Hence, when considering a soil profile of 150 cm, 2500 kg N/ha/5months is not so unreasonable anymore.
What could be the reason for possible overestimating N2O production and consumption? I think it could be the fact that you assume open system dynamics for isotopic fractionation during N2o reduction. I recall we had a discussion on this after the Decock & Six review in 2013 and my impression was that later on most authors assumed that closed system dynamics are more probable for soil denitrification. In the study of Lewicka-Szczebak, D., et al. (2017). "Quantifying N2O reduction to N2 based on N2O isotopocules – validation with independent methods (helium incubation and 15N gas flux method)." Biogeosciences 14(3): 711-732. this could be confirmed by independent measurement of N2 fluxes, since a match of NA isotopes and 15N-tracing was only obtained when assuming closed system dynamics. To illustrate the huge difference in calculated N2O reduction when using closed or open system dynamics one might use the equations for closed and open system fractionation shown in in Decock and Six 2013 and calculate SP using the unreduced fraction of N2O (f) of e.g 0.02 according to Monte Calme treatment in Table 5, giving for open system: SP = SP0 - εSP (1 - f) = -2.4permil - (-5.3permil) * (1-0.02) = 2.8 per mil; for closed system: SP = SP0 + εSP * ln(f) = -2.4permil + (-5.3permil) * ln(0.02) = 18.3 permil. So this shows the huge difference of both approaches for small f values, while results are more similar for f values close to 1. Looking at the SP value of open system dynamics yielding f = 0.02 we can check which f value would be obtained by closed system dynamics if we solve the equation for f giving: f = exp((SP-SP0)/eSP) = 0.38. This shows that closed system would lead to much higher N2O/(N2+N2O ) ratios. Strong overestimation of N2O reduction due to open system assumption would also explain the very high N2Onit values: if the combination of SP and d18O values yields a fraction from nitrification of say 30%, then with the large values of total N2O consumption you end up with these high numbers for N2Onit. So possibly, by assuming closed system dynamics you would solve this contradiction.
We appreciate the reviewer’s reflection, but kindly disagree that there is evidence for N2O production and consumption to be overestimated in our study. While there is no true validation of our model results, we argue in the discussion section of the manuscript and responses to other comments that our findings are well within the roam of what has been found in the literature. We do acknowledge, however, that this is a proof-of-concept study and future research should continue to improve and validate our proposed modeling approach. We also fully agree that the issue of open vs. closed system dynamics needs to be addressed, and provided details on how this will be addressed in the revised manuscript in responses to other comments.
Some more detailed discussion how N2O consumption could be larger than production would be helpful.
We refer the reviewer to responses to comments posed by other reviewers. We will edit the revised manuscript accordingly.
I was astonished about another number: bulk density of > 1.7 after sieving and packing. How in the world did you achieve this with sieved loamy soil? I think it is only possible with extreme compaction and I wonder how wheat could grow. If you used indeed extreme compaction procedure then you might report why you chose this and how it was achieved. With BD about 1.7, diffusivity must have been extremely low during moist phases and thus could indeed explain extreme denitrification rates. I think the paper would gain if you discussed the uncertainty from calculated diffusivity and assuming constant BD. You might also consider that for low air filled porosity (as maybe in your case ) there are special equations for Ds (eg Sallam, A., et al. (1984). "Measurement of Gas Diffusion Coefficient under Relatively Low Air-filled Porosity." Soil Science Society of America Journal 48(1): 3-6)
We acknowledge that the bulk density measured in our lysimeters is very high. We triple checked our calculations and noted that the bag weight had not been subtracted. After this correction, the bulk density was still relatively high at 1.64 g/cm3. As discussed in our response to another comment, the high bulk density is likely due to settling and compaction of the soil over the 7-month period, where repeated watering may have caused slaking and compaction. The bulk density may also have been inflated by the measurement procedure, using a sliding hammer core to take soil samples. We recognize the importance of a good bulk density estimate for diffusion modeling. Given that this is a proof-of-concept study, we plan to rerun the model with the updated bulk density value and do a sensitivity analysis on how the model outcomes respond to bulk density in the revised manuscript.
But irrespective of the question whether my concerns are justified or not, I think your approach is really promising. Would be nice if someone would check its outcome using independent methods soon. I always found this very helpful when evaluating new denitrification methods.
We fully agree with the reviewer. We underline that his is a proof-of-concept study and hope our work will inspire future research in this field. There are many opportunities for further model development. We will highlight that in the revised manuscript.
References
Booth, M.S., Stark, J.M., Rastetter, E., 2005. Controls on nitrogen cycling in terrestrial ecosystems: A synthetic analysis of literature data. Ecological Monographs 75, 139-157.
Decock, C., Six, J., 2013. An assessment of N-cycling and sources of N2O during a simulated rain event using natural abundance 15N. Agriculture, Ecosystems & Environment 165, 141-150.
Citation: https://doi.org/10.5194/bg-2022-221-AC2
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RC2: 'Comment on bg-2022-221', Anonymous Referee #2, 11 Jan 2023
The manuscript bg-2022-221 reports on a model concept to calculate total denitrification based on natural abundance N2O isotopic composition. This is an extremely important subject that has remained a challenge especially due to the complications in measuring N2 emissions. From this perspective, this study is an important contribution for the scientific community, is well placed in a journal like BG and in my opinion definitely deserves publication.
The study is extremely well structured and written, so that formal comments hardly arise. However, there are some aspects that need to be considered:
- The presentation of available data is not complete. Soil-atmosphere flux rates of N2O were determined using static chambers, but the time series of N2O emission is not shown and only used to calculate cumulative emission. Are there any emission peaks after fertilizer applications? Is there an emission event between day 80 and 100 when soil N2O concentration shows a peak (Figure 2a)? Diffusion fluxes for the top of soil compartment 1 could be easily (and should be) plotted together with measured N2O emissions. Time series of the production/consumption rates in the various depths would also be informative. Fertilizer application dates are not shown in figures, which is a pity.
- A major point is that N2O consumption is consistently larger than N2O production. Does this mean that layer 1 takes up N2O? From this perspective, it appears quite nonrational to not assess the influence of constraining the model with an alternative upper boundary condition. At the moment, a constant concentration boundary is applied at the upper end of the soil profile. I ask the authors to use a flux boundary at the top of layer 1 and investigate in how far this procedure changes results. Additionally, a sensitivity analysis could hep to find a parameter set that allows for N2O emissions while estimating sound N2O production rates
- I am not sure if the concept of smooth functions is really adequate. N2O production in soil, and, thus N2O emission is notorious for its episodic behaviour. From this perspective, short-term increase in soil air N2O concentrations will be associated with flux events. Using smooth functions will suppress all short-term behaviour as these events are neglected by smoothing algorithms. This also refers to figure 2a (see point 1), which is obviously suppressed by the smooth functions. àAfter having read the manuscript again, I am not even sure if I understand what the authors mean exactly with smooth functions. In the first moment I thought the aim was to fit a function that is analytically differentiable. But I have the impression that the derivatives were formed numerically? Please clarify.
- Maybe the most important point is that the state equations are not unconditionally physically sound. For instance, the mixing term in equations 7 and 8 is not constrained mathematically. Just consider a situation in which N2Onit is four times larger than the stored N2O concentration and SP0 is 0. Then the shift in SP would be something like 120 per mil which is impossible as the shift has to be limited to SPnit-SP0. I am aware that the authors have derived this simplification under the assumption that Dtà0, but this is not forced in the numerics. This means that a time step control function / criterion needs to be defined. Or the independence of the solution of Dt needs to be shown (plot of solutions for different Dt).
- There is no validation data for the model at all. The only available information is N2O flux rate. N2O flux rates show emission of N2O from the soil while the model result suggests constant? N2O consumption. In absence of other validation parameters, the message that the model produces reasonable results is not convincing. What parameter changes are necessary to obtain N2O emission from the top layer and what conclusions for the model concept follow from this?
Please find details below.
Title
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Highlights
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Abstract
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Introduction
Materials and Methods
L135: Please check bulk density value. It is a quite high value and rather unlikely to result from repacking unless massive pressure was applied during the process.
L209: Not using available surface fluxes seems nonrational to me. It is a direct constraint and could be used directly for the later described equations 6, 7 and 8 for the top layer.
L208: please clarify what semi-independent means in this context.
L214-216: was the system of linear equations formulated in a way that there is one system per layer or was there one system for all layers combined?
L223: It may be pertinent to add that concentration C is in volume per volume, i.e., m3 m-3?
L225: please check value. It is quite impossible that a greenhouse is able to maintain a mixing ratio so much lower than atmospheric mixing ratio. Or is this an uncalibrated raw reading?
Section 2.5.3: I have some problems with the smooth functions. I think I perfectly understand why the authors have chosen smooth functions, since they are unconditionally differentiable at any point in time, however, isn’t the essence of N2O emission its notoriously episodic character? And can this episodic character be reproduced by smooth functions? In view of Figure 2a, I think that important aspects like a possible emission peak between day 80 and 100 could have been overlooked by selecting smooth functions.
L248-254: This paragraph is rather incomprehensible: What does “All data values are averaged at each time step of measurements and then indexed by time” mean? If measurements are 8 hours apart from each other and equidistant, were measurement time +- 4 hours averaged? Or do the authors refer to the replicate lysimeters?
Was the most suitable smoothing function the one with the lowest sum of square error of fit?
Please explain time series bootstrapping. I don’t see how the uncertainty of the transient N2O concentration in a layer can be obtained by time series bootstrapping.
Equations (8) and (9): These equations are used to reflect both isotopic fractionation and mixing. However, the mixing part is necessarily mass / isotope conserving. I.e., it is only a valid approximation if Ftop, Fbot, N2Onit, N2Oden and N2Ored are small compared to N2Oconc,0. The reason is as follows: Assume that in (7), N2Onit 4 times N2Oconc,0 and SP0 is 0. The shift in SP would be 4 *34.4 per mil = 137.6 per mil. This is outright impossible. Consequently, the formulation as it is doesn’t ensure a physically sane mixing process as the highest possible shift would be limited to a shift that results in SP of 34.4 per mil for nitrification-derived N2O and 0 for denitrification. This means, the authors need to find criterions for the time step control or find a formulation that allows simultaneous fractionation and mixing calculations in a mathematically correct way.
L284: diffusion isotope effects have different sign and massively different magnitude. How can the isotope effect of diffusion be so different if the mass difference between 14N15N16O and 14N14N18O is only in the range of 1/46 ~ 2.1%? Considering the low inverse isotope effect of diffusion for SP and the inverse sign of d18O, I am wondering if these isotope effects are robust.
L310-313: I fully agree that at small time steps, open and closed system calculations yield the same results. However, the adequate time step size depends on magnitudes of flux rates, N2O concentration and isotope effect. The authors have to at least show that results did not change significantly for different time steps or present a time step control.
Results
L339: 0 to 30 ppm is a huge range. Were there amount effects, i.e., an effect of N2O mixing ratio on isotopic composition? Was this checked in any way? Please refer to it in your methods section.
L348: please change second “where” to “were”.
L352-354: it actually seems like a stark contrast to pulse emissions, but in the paper, I could not find soil-atmosphere N2O flux. Could you please provide the time series of the chamber flux measurements and integrate it in the publication?
L400: The uncertainty analysis is important, and very much appreciated. However, I am confused when looking at Figure 3. It seems like all variations in endmembers and input variables will result in lower production or consumption rates when rates are higher than 0.3 kg ha-1 day-1. Please explain this behavior. I assumed to see both positive and negative deviations. Is the used parameter set some unique constellation of values?
At lower rates, the model doesn’t seem robust (see values after day 100) at which relative deviation of fitted rates are massive. This needs to be discussed.
Discussion
L460-462: whether or not soils are net sinks or sources for N2O is a fundamentally important question. The model results of net N2O uptake from the atmosphere contradict the observation of typical N2O emission rates. At this point, the authors need to further investigate possible reasons. One striking aspect is already shown in Figure 3: Nitrification- and denitrification-related N2O emissions were lower if uncertainty in endmembers or input variables (bulk density, soil moisture, N2O concentrations and isotopic composition) was considered. This may indicate that different endmembers or input parameters may decrease the discrepancy of gross production and consumption. The model should for sure be constrained in a way that the surface fluxes are reproduced by the model.
In addition, the figures lack indication of fertilizer application. Was fertilizer application associated with soil-atmosphere fluxes?
L497-499: Decoupling is one possibility, but alternatively, N2O production pulses in a top soil layer may be concealed due to the low sampling rate. This may be a consequence of the shorter travelling time of a N2O molecule that is produced close to the soil-atmosphere boundary. Higher soil moisture at lower depths may decrease transport rates out of the soil.
Conclusion
L527-528: I don’t agree that your model has necessarily constrained total denitrification, especially since total soil-atmosphere exchange could not be reflected. Your study has definitely shown that N2O production needs to be largely balanced by consuming processes. But you could not show in how far the solutions are accurate with regard to magnitude of fluxes.
Supporting information
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Citation: https://doi.org/10.5194/bg-2022-221-RC2 -
AC3: 'Reply on RC2', Charlotte Decock, 14 Mar 2023
We thank the reviewers for their constructive and thorough comments. Please find reviewer comments followed by author response to each column below. Author responses are shown in bold.
The manuscript bg-2022-221 reports on a model concept to calculate total denitrification based on natural abundance N2O isotopic composition. This is an extremely important subject that has remained a challenge especially due to the complications in measuring N2 emissions. From this perspective, this study is an important contribution for the scientific community, is well placed in a journal like BG and in my opinion definitely deserves publication.
The study is extremely well structured and written, so that formal comments hardly arise. However, there are some aspects that need to be considered:
The presentation of available data is not complete. Soil-atmosphere flux rates of N2O were determined using static chambers, but the time series of N2O emission is not shown and only used to calculate cumulative emission. Are there any emission peaks after fertilizer applications? Is there an emission event between day 80 and 100 when soil N2O concentration shows a peak (Figure 2a)? Diffusion fluxes for the top of soil compartment 1 could be easily (and should be) plotted together with measured N2O emissions. Time series of the production/consumption rates in the various depths would also be informative. Fertilizer application dates are not shown in figures, which is a pity.
We appreciate the reviewer’s recognition of the richness of the dataset. The paper already has 5 figures and 5 tables, so we opted not to show time series of N2O production and consumption for each treatment and depth increment. Likewise, we opted not to include a comparison of the diffusion fluxes for the surface layer and daily N2O surface fluxes measured using the closed chamber technique, as it is not the major focus of the study. Several previous studies have made such comparisons, and generally conclude that there are discrepancies between the methods. Likely, the diffusion gradient method is unable to assess N2O dynamics in the very top few cm of the soil. We acknowledge, however, that providing the additional data may be valuable to the community and will provide the additional charts in supporting information in the revised manuscript. In addition, we will provide an R markup file with the core of the code and a file with the raw N2O concentrations and isotope values of N2O at each depth for each lysimeter over the course of the experimental period. This can support further advancement of models concerned with N2O dynamics in the soil profile.
A major point is that N2O consumption is consistently larger than N2O production. Does this mean that layer 1 takes up N2O?
N2O consumption is consistently larger than N2O production because the N2O concentration in the soil profile at the start of the experiment is greater than the N2O concentration in the soil profile at the end in the lower 3 depth increments. Potentially, N2O built up prior to the start of the experiment as soil was repacked and wetted, followed by a slow net consumption over the course of the experiment. Note that the difference between N2O production and consumption is relatively small and not significant when considering variation across replicates. It should be noted that N2O flux rates are generally 1000 times smaller than other gross N transformation rates in the N cycle. Our study suggest that gross N2O production and consumption rates may be more in the range of other gross N transformation rates, which exemplifies why it is so hard to accurately measure N2O surface fluxes. We acknowledge that future model development may reduce uncertainty and add additional constraints to the model to address this issue.
From this perspective, it appears quite nonrational to not assess the influence of constraining the model with an alternative upper boundary condition. At the moment, a constant concentration boundary is applied at the upper end of the soil profile. I ask the authors to use a flux boundary at the top of layer 1 and investigate in how far this procedure changes results.
We thank the reviewer for this suggestion. Given that this analysis would add a significant amount of work, we suggest this would be a great subject for future research. We will make note of this suggestion in a section on recommendations for future developments in the revised manuscript.
Additionally, a sensitivity analysis could hep to find a parameter set that allows for N2O emissions while estimating sound N2O production rates
We do not believe our gross N2O production rates are unsound. Likely, the challenge lies in gross N2O production and consumption rates being effectively orders of magnitude greater than net N2O surface fluxes, complicating model development for good estimations of both gross N2 loss and N2O surface emissions. Future model development should focus on this issue.
I am not sure if the concept of smooth functions is really adequate. N2O production in soil, and, thus N2O emission is notorious for its episodic behaviour. From this perspective, short-term increase in soil air N2O concentrations will be associated with flux events. Using smooth functions will suppress all short-term behaviour as these events are neglected by smoothing algorithms. This also refers to figure 2a (see point 1), which is obviously suppressed by the smooth functions. After having read the manuscript again, I am not even sure if I understand what the authors mean exactly with smooth functions. In the first moment I thought the aim was to fit a function that is analytically differentiable. But I have the impression that the derivatives were formed numerically? Please clarify.
We agree with the reviewer that surface N2O fluxes are notorious for their high temporal and spatial variability leading to hot moments and hotspots. To date, however, studies that have measured subsurface N2O concentrations have not observed this type of behavior. In addition, the goal of the study is not to accurately estimate the temporal variability in N2O surface emissions, but to estimate gross N2 loss over the soil profile. In this context, we believe fitting a smooth curve to the data is appropriate. The current fits to the subsurface data include a linear model, a cubic spline, and a loess function. To determine derivatives, we calculated the slope to the fitted curve for discrete time points. Future model development will focus on developing smooth curves capable of more closely capturing temporal variation in the data, for example by using different versions of Gaussian processes to smooth measurements or source contributions directly.
Maybe the most important point is that the state equations are not unconditionally physically sound. For instance, the mixing term in equations 7 and 8 is not constrained mathematically. Just consider a situation in which N2Onit is four times larger than the stored N2O concentration and SP0 is 0. Then the shift in SP would be something like 120 per mil which is impossible as the shift has to be limited to SPnit-SP0. I am aware that the authors have derived this simplification under the assumption that Dtà0, but this is not forced in the numerics. This means that a time step control function/criterion needs to be defined. Or the independence of the solution of Dt needs to be shown (plot of solutions for different Dt).
Thank you for this comment. We would like to emphasize that the model is not meant to be a simulation model. We do not aim to estimate the shift in isotope values over time by parameterizing process rates. Instead, we discretize time series of patterns in N2O concentrations and isotope values to estimate N2O production and consumption rates at each time point. Thus, the rates are nearly independently estimated at each time point based on observed patterns in N2O concentrations and isotope values, along with isotope end-members for N2O production and consumption processes characterized in the literature. Our model has 3 unknowns, namely gross N2O production by nitrification, gross N2O production by denitrification, and gross N2O consumption, and 3 equations. A solution for the system of equations is sought at each time point. We acknowledge that including more source processes or isotopic constraints may improve the model in future iterations, but this is outside of the scope of the current study.
There is no validation data for the model at all. The only available information is N2O flux rate. N2O flux rates show emission of N2O from the soil while the model result suggests constant? N2O consumption. In absence of other validation parameters, the message that the model produces reasonable results is not convincing. What parameter changes are necessary to obtain N2O emission from the top layer and what conclusions for the model concept follow from this?
We acknowledge that there is no true validation of the model results. However, no method currently exists that adequately estimates gross N2O production in the soil profile, rendering a true validation impossible. As discussed in the manuscript, all methods have their flaws, and we know quite little about gross N2 production rates. Studies targeting denitrifier genes in the soil profile consistently find high abundances, suggesting denitrification is indeed ubiquitous in the soil. In our discussion, we invite the readers to open their minds to the idea that total denitrification, in some soils, may be greater than previously thought. It should be emphasized that our model is a proof-of-concept study. In future studies, it would be valuable to compare gross N2 production rates based on this approach with other methods, particularly compared to 15N tracers methods and direct N2 quantification under low N2 atmosphere. We also note that the model does not aim to estimate surface N2O fluxes based on subsurface N2O dynamics. In contrast, the main aim of our approach is to estimate total N2 loss. In this context, we argue that gross N2O production and consumption rates likely operate at a different order of magnitude compared to surface fluxes, possibly shedding some light on why accurately measuring and simulating surface N2O emissions has been so challenging.
Please find details below.
Materials and Methods
L135: Please check bulk density value. It is a quite high value and rather unlikely to result from repacking unless massive pressure was applied during the process.
We agree with the reviewer that the bulk density measured in our experiment is quite high. It should be noted that the experiment was set up in 1.5m tall and 0.5 m diameter lysimeters. The repacked soil was watered and allowed to settle and equilibrate for two months before the start of the experiment. It is possible that heavy disturbance of soil during repacking followed by sequential deep waterings of the lysimeters caused slaking of aggregates and compaction. Furthermore, bulk density was assessed at the end of the experiment, at which point the soil had been in the lysimeters for 7 months. During destructive sampling, a sliding hammer soil core was used the collect ‘undisturbed’ soil cores with known volume. Some additional compaction may have happened during the sampling procedure. The soil felt notable compacted during destructive sampling. Finally, the soil has a relatively high sand content (58%) and low soil organic carbon (0.08% in topsoil and 0.04% in subsoil), both of which generally results in higher bulk density.
L209: Not using available surface fluxes seems nonrational to me. It is a direct constraint and could be used directly for the later described equations 6, 7 and 8 for the top layer.
We appreciate the suggestion but given the well documented mismatch between surface fluxes and fluxes based on the gradient method, we do not believe this is a good approach for estimating gross N2 production in the soil profile. The commonly observed mismatch between N2O surface fluxes based on the gradient method and flux chamber measurements suggests at least a partial decoupling of N2O dynamics in the very top few cm of soil relative to the rest of the profile. Given that the focus of this study is to constrain N2 production in the soil profile, we do not believe that surface fluxes would help in constraining the model.
L208: please clarify what semi-independent means in this context.
We mean that the only relationship between two time points is the smooth curve. The smooth curve aims to fit the pattern in the data over time as well as possible without making assumptions about underlying mechanisms or reaction kinetics. Its only purpose is to be able to estimate the infinitesimal change in the concentration or isotope value at each time point, using the first derivative. The gross N2O production and reduction rates are estimated separately for each time point and depth increment. Therefore, we consider the estimates at each time point semi-independent. We will specify this accordingly in the revised manuscript.
L214-216: was the system of linear equations formulated in a way that there is one system per layer or was there one system for all layers combined?
There was one system per layer. We will specify this accordingly in the revised manuscript.
L223: It may be pertinent to add that concentration C is in volume per volume, i.e., m3 m-3?
Thank you for this suggestion, we will implement the change accordingly in the revised manuscript.
L225: please check value. It is quite impossible that a greenhouse is able to maintain a mixing ratio so much lower than atmospheric mixing ratio. Or is this an uncalibrated raw reading?
This was an uncalibrated raw reading. We are sorry for this oversight and will make necessary edits to the manuscript.
Section 2.5.3: I have some problems with the smooth functions. I think I perfectly understand why the authors have chosen smooth functions, since they are unconditionally differentiable at any point in time, however, isn’t the essence of N2O emission its notoriously episodic character? And can this episodic character be reproduced by smooth functions? In view of Figure 2a, I think that important aspects like a possible emission peak between day 80 and 100 could have been overlooked by selecting smooth functions.
The reviewer is correct in guessing that our choice for the smooth functions is that they are unconditionally differentiable at any point in time. As noted earlier, we agree that N2O is notoriously temporal variable when it comes to surface fluxes, but N2O subsurface concentrations published to date do not seem to follow the same trend. Patterns in subsurface N2O concentrations tend to change much more slowly over time. In our data set, there is one exception, in the 7.5 cm depth layer in one of the lysimeters. We argue that this one observation may be an outlier.
L248-254: This paragraph is rather incomprehensible: What does “All data values are averaged at each time step of measurements and then indexed by time” mean? If measurements are 8 hours apart from each other and equidistant, were measurement time +- 4 hours averaged? Or do the authors refer to the replicate lysimeters?
We thank the reviewer for pointing out the ambiguity in this phrasing and will edit as needed in the revised manuscript. Diffusion fluxes are calculated based on the observed N2O concentrations at each time point of observation. This was done for each lysimeter and each depth increment individually. Then, smooth functions were fit for each depth and lysimeter for diffusion fluxes, N2O concentrations, and isotope values. Smooth functions were indexed by time on a daily time step over the course of the experimental period, and derivatives and predicted values were determined for each day. As such, the system of equations was solved for each day, while original data was collected on a weekly basis, but the smooth functions interpolated between measurements days. We hope this clarification helps.
Was the most suitable smoothing function the one with the lowest sum of square error of ifit?
If the loess or base spline fit were not significantly different from the linear model, a linear fit was assumed. Choice between base spline and loess fit was based on visual observations of how well the predicted data fit the observations. Future model development could improve upon the smooth fitting of the observed data.
Please explain time series bootstrapping. I don’t see how the uncertainty of the transient N2O concentration in a layer can be obtained by time series bootstrapping.
We will describe how time series bootstrapping was performed in our specific case in more detail in the revised manuscript. Briefly, time series bootstrapping was applied to calculate the standard error of the fitted values for N2O fluxes averaged at each time step for the smooth curve. Here, we considered general bootstrapping with a fixed block that generates replicate time series (e.g., 1000 times). Then the 95% confidence interval of estimated fluxes was computed, accordingly.
Equations (8) and (9): These equations are used to reflect both isotopic fractionation and mixing. However, the mixing part is necessarily mass / isotope conserving. I.e., it is only a valid approximation if Ftop, Fbot, N2Onit, N2Oden and N2Ored are small compared to N2Oconc,0. The reason is as follows: Assume that in (7), N2Onit 4 times N2Oconc,0 and SP0 is 0. The shift in SP would be 4 *34.4 per mil = 137.6 per mil. This is outright impossible. Consequently, the formulation as it is doesn’t ensure a physically sane mixing process as the highest possible shift would be limited to a shift that results in SP of 34.4 per mil for nitrification-derived N2O and 0 for denitrification. This means, the authors need to find criterions for the time step control or find a formulation that allows simultaneous fractionation and mixing calculations in a mathematically correct way.
Please see response in attachement. Our response includes equations that did not carry over well in the embedded response box.
L284: diffusion isotope effects have different sign and massively different magnitude. How can the isotope effect of diffusion be so different if the mass difference between 14N15N16O and 14N14N18O is only in the range of 1/46 ~ 2.1%? Considering the low inverse isotope effect of diffusion for SP and the inverse sign of d18O, I am wondering if these isotope effects are robust.
Thank you for this comment. We adopted isotope effects associated with diffusion from the literature. However, verifying the likelihood of the isotope effect of N2O diffusion is outside of the scope of this study. Future research could further investigate this matter.
L310-313: I fully agree that at small time steps, open and closed system calculations yield the same results. However, the adequate time step size depends on magnitudes of flux rates, N2O concentration and isotope effect. The authors have to at least show that results did not change significantly for different time steps or present a time step control.
We thank the reviewer for this suggestion. The change in N2O concentrations and isotope values over time is reflected in the derivative to the smooth curve at that time point. The system of equations was solved at each time point for which the derivative was calculated, which was chosen to be every day. However, as the smooth curve integrates between originally observed time points, the model outcome would not change if we changed the time step at which the system of equations is solved. There would just be less points in figures 3 and 4.
Results
L339: 0 to 30 ppm is a huge range. Were there amount effects, i.e., an effect of N2O mixing ratio on isotopic composition? Was this checked in any way? Please refer to it in your methods section.
Concentration dependencies during the measurement of the isotopic composition of N2O are overcome by tuning the IRMS to be linear across a range of concentrations. However, the IRMS in our lab is optimized for measuring a range between 0.3 to 3ppm. Therefore, concentrations higher than 3ppm were diluted down to be able to measure them accurately on the device.
L348: please change second “where” to “were”.
We will implement this change in the revised manuscript.
L352-354: it actually seems like a stark contrast to pulse emissions, but in the paper, I could not find soil-atmosphere N2O flux. Could you please provide the time series of the chamber flux measurements and integrate it in the publication?
We will include the time series of the N2O flux in supplementary materials.
L400: The uncertainty analysis is important, and very much appreciated. However, I am confused when looking at Figure 3. It seems like all variations in endmembers and input variables will result in lower production or consumption rates when rates are higher than 0.3 kg ha-1 day-1. Please explain this behavior. I assumed to see both positive and negative deviations. Is the used parameter set some unique constellation of values? At lower rates, the model doesn’t seem robust (see values after day 100) at which relative deviation of fitted rates are massive. This needs to be discussed.
We will expand on the sensitivity analysis in the revised manuscript and test the impact of uncertainty around endmembers in several depths and lysimeters, to provide a more comprehensive overview of whether this behavior is systematic or not. We will also redo all analysis to include the most current end-member values published in Yu et al. 2020. The discussion will be elaborated on accordingly.
Discussion
L460-462: whether or not soils are net sinks or sources for N2O is a fundamentally important question. The model results of net N2O uptake from the atmosphere contradict the observation of typical N2O emission rates. At this point, the authors need to further investigate possible reasons. One striking aspect is already shown in Figure 3: Nitrification- and denitrification-related N2O emissions were lower if uncertainty in endmembers or input variables (bulk density, soil moisture, N2O concentrations and isotopic composition) was considered. This may indicate that different endmembers or input parameters may decrease the discrepancy of gross production and consumption. The model should for sure be constrained in a way that the surface fluxes are reproduced by the model.
We agree with the reviewer that whether soils are a net source or sink of N2O is an important issue. We will explore the impacts of changing bulk density or end members in more detail in the revised manuscript and elaborate on it in the discussion. Meanwhile, we argue that N2O surface fluxes and gross N2 production operate at different orders of magnitude, and that different approaches may be needed to unravel these two research gaps in more detail. The focus of this study was to propose a method to estimate gross N2 loss from the soil profile, in the context of constraining ecosystem N budgets. If the focus is to estimate net N2O fluxes from the surface, flux chambers or eddy covariance methods are much more direct measurements and therefore more appropriate.
In addition, the figures lack indication of fertilizer application. Was fertilizer application associated with soil-atmosphere fluxes?
We will include surface fluxes and indications of fertilizer application in supporting information in the revised manuscript.
L497-499: Decoupling is one possibility, but alternatively, N2O production pulses in a top soil layer may be concealed due to the low sampling rate. This may be a consequence of the shorter travelling time of a N2O molecule that is produced close to the soil atmosphere boundary. Higher soil moisture at lower depths may decrease transport rates out of the soil.
We will add this suggestion to the revised manuscript.
Conclusion
L527-528: I don’t agree that your model has necessarily constrained total denitrification, especially since total soil-atmosphere exchange could not be reflected. Your study has definitely shown that N2O production needs to be largely balanced by consuming processes. But you could not show in how far the solutions are accurate with regard to magnitude of fluxes.
We will change the phrasing to reflect this comment in the conclusion of the revised manuscript.
Interactive discussion
Status: closed
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RC1: 'Comment on bg-2022-221', Anonymous Referee #1, 23 Dec 2022
Dear authors, dear editors
General comments:
This is an interesting and important paper on soil N2O dynamics, including detailed insight into its production and consumption processes along the soil profile. Although the method presented relies on multiple assumptions I think this is a very interesting approach allowing for a better understanding of N2O origins and sinks. I mostly wonder if this approach can be transferred to the real field conditions. Since you used sieved and homogenized soil, the diffusion can be easily fitted and you do not deal with inhomogeneity issues. For example, by intact soil profiles, you would need to have individual values regarding density, moisture, or d18O of soil water for each layer. This experiment was carried out in a greenhouse, how would wind impact your modelling procedure? A discussion on the possible perspective of transferring this method to the field would be a valuable issue in your manuscript, so I would suggest adding this.
I have also some doubts about the calculations. In the appendix you made some simplifications of the equations which are not justified and difficult to follow. Please expand your explanations, in below specific comments I have indicated what exactly I’ve found unclear.
Specific comments:
Please use delta symbols in your manuscript.
L79 – Recently published method for applying 15N tracer in field in N2-depleted atmosphere should be mentioned here (Well et al., 2019, RCM 33: 437-448). This is a compromise overcoming difficulties associated with 15N tracing (lower 15N levels can be applied, better sensitivity in N2-depleted atmosphere) and N2-free atmosphere experiments (it can be applied in field conditions!)
L83 – Also for natural abundance N2O analyses an important progress has been achieved recently, Lewicka-Szczebak et al., 2020 (BG 17 (22): 5513-5537) proposed a modelling approach based on all 3 isotopic signatures of N2O. It was validated for field conditions application and can provide quantification of N2O reduction also providing uncertainity assessment.
L250 tests were included
L269 you need to define how eta values are defined and which values you applied for them
Table 1 – there is new review paper by Yu et al, 2020 (RCM 34 (20): e8858, appendix) summarising the values, it would be most up to date to cite these (there are some important changes in the ranges)
L 286 you say that there is a common range for nitrification and fungal denitrification – in the most recent review (Yu et al., 2020) it has been shown that the d18O for nitrification should be slightly different than assumed in previous publications, you should either decide which of these processes is more relevant for your study or assume a slightly wider range for d18O
Eq 7,8 – eta*F reduced/diffused – you make open system assumption in your equations – definitely right for diffusion, but can be doubt for N2O reduction, there might be values which cannot be explained with open system equation (Lewicka-Szczebak et al., 2014, 2017), or you can wrongly attribute this to larger proportion of nitrification. Especially given that you have large reduction it makes big difference if using open or closed system equations. I would check what is the difference and report this. You have only justified using the open system equation with the argument of simplified maths, but I think this generates significant bias. The requirement for using open system equation is the equilibrium of the fluxes in and out (Fry, 2006) and you clearly do not have this between N2O production and reduction.
Did you take into account atmospheric N2O diffusing into the soil? Have you sampled ambient air for N2O isotopic analyses?
L 555 (Appendix) – “With various terms cancelling out, the equation can be rewritten as:” – why can you cancel out “various things”, what are these “various things” and how this cancelling out influences the final result?
L563 (Appendix) – “For ât approaching 0, the equation can be further simplified as:” – why can you assume Dt approaching 0? It is one day, right? When you are using fluxes in your equations you need the time factor to be included in the equations, I guess. What are the units for the fluxes used in your Eq 7 and 8?
Table 3 You have given the N2O fluxes without time units. For which time period are the amounts given (per hour, per day?)
Table 5 – same as above
L355-357 – I am not sure if Fig 1 really supports this statement. For some isotopic signatures you have really large variations within the 2 weeks time, eg. SP values 7.5cm depth
L361 – very low SP – cannot be explained with any known literature data?! Can this be due to some measurement or evaluation problem? As these are individual samples you should carefully look on their measurements – was the N2O concentration in good range? Check your normalisation procedure for evaluation of SP data. What is your lowest SP standard? If your lowest standard value is near atmospheric air (eg. +18) then your normalisation for such low values may produce large offset (see Mohn et al, 2014).
You also have d15N data, why not using them in the modelling as well? Maybe then can be useful in distinguishing further processes like nitrification and fungal denitrification (in case you would also analyse the substrates).
Fig 3b, 3c – why there are no error bars for the points before day20 and after day100?
Section 2 – have you analysed d18O of soil water? If so, please describe, which method, how many samples etc. If not, please justify your assumption on -9.9 permil.
Citation: https://doi.org/10.5194/bg-2022-221-RC1 -
AC1: 'Reply on RC1', Charlotte Decock, 14 Mar 2023
We thank the reviewers for their constructive and thorough comments. Please find reviewer comments followed by author response to each column below. Author responses are shown in bold.
Dear authors, dear editors
General comments:
This is an interesting and important paper on soil N2O dynamics, including detailed insight into its production and consumption processes along the soil profile. Although the method presented relies on multiple assumptions I think this is a very interesting approach allowing for a better understanding of N2O origins and sinks. I mostly wonder if this approach can be transferred to the real field conditions. Since you used sieved and homogenized soil, the diffusion can be easily fitted and you do not deal with inhomogeneity issues. For example, by intact soil profiles, you would need to have individual values regarding density, moisture, or δ18O of soil water for each layer. This experiment was carried out in a greenhouse, how would wind impact your modelling procedure? A discussion on the possible perspective of transferring this method to the field would be a valuable issue in your manuscript, so I would suggest adding this. I have also some doubts about the calculations. In the appendix you made some simplifications of the equations which are not justified and difficult to follow. Please expand your explanations, in below specific comments I have indicated what exactly I’ve found unclear.
We greatly appreciate the reviewer’s positive evaluation of the importance of our work and the constructive comments and suggestions to further improve our modeling approach. The paper we present is a proof-of-concept study. To the greatest extent possible, we will integrate suggestions and recommendations in the revised manuscript. Nevertheless, we found some suggestions and comments are beyond the scope of this study, and present great opportunities for future research and development. Details are outlined below.
We acknowledge the reviewer’s concern about transferability of the modeling approach to a field situation and will include text in the discussion section addressing important considerations for field applications. Any previous research on limitations of diffusion models in a field setting would apply to this study as well, but are beyond the scope of this work. We appreciate the reviewer’s suggestion of recommending depth differentiated measurements of bulk density, soil moisture, and δ18O of soil water. The current model already includes depth and time differentiated values for soil moisture based on in-situ measurements. Bulk density was not significantly different between depth increments in our experiment. Adding depth differentiated bulk density and δ18O of soil water can easily be done in future projects.
As to the question of how wind would impact the modeling outcomes, we can only speculate. We acknowledge that wind causes pressure differences at the soil surface which will affect the flux. However, one can argue how well impacts of wind are captured in published N2O flux data from field trials. When fluxes are measured using static flux chambers, the surface in the chamber will be sheltered from the wind by the chamber and wind effects may be missed. Studies that compare N2O surface fluxes measured using static flux chambers with N2O flux estimated based on the diffusion gradient method consistently see discrepancies between the two methods. Flux measurements using static flux chambers often show hot moments, characterized by brief but sharp pulses in N2O emissions. The gradient method does not commonly show equally sharp pulses in N2O concentrations in the subsurface, thereby failing to predict the surface to atmosphere N2O flux accurately. We believe that surface and subsurface N2O dynamics may be decoupled, and that the hot moments often observed in surface fluxes may be produced in the top few cm of soil, above the point where the shallowest diffusion sampler may be installed. Given that our method primarily aims to estimate total denitrification throughout the profile based on N2O concentrations and isotope values in that profile, combined with many observations in the literature that suggest at least a partial decoupling of surface and subsurface N2O dynamics, we would expect the impact of wind on our estimates of total denitrification in the soil profile to be relatively low.
Based on detailed comments of the reviewer on the proof for the equations used in the model, we will add a more detailed description in the appendix of the revised manuscript where the proof is delineated.
Specific comments:
Please use delta symbols in your manuscript.
We assume that the reviewer is referring to delta symbols for shown isotope values. We tried to refer to all isotope values with delta symbols but will check the manuscript again thoroughly if this was accidently not done.
L79 – Recently published method for applying 15N tracer in field in N2-depleted atmosphere should be mentioned here (Well et al., 2019, RCM 33: 437-448). This is a compromise overcoming difficulties associated with 15N tracing (lower 15N levels can be applied, better sensitivity in N2-depleted atmosphere) and N2-free atmosphere experiments (it can be applied in field conditions!)
We will acknowledge the newly proposed method in the revised manuscript.
L83 – Also for natural abundance N2O analyses an important progress has been achieved recently, Lewicka-Szczebak et al., 2020 (BG 17 (22): 5513-5537) proposed a modelling approach based on all 3 isotopic signatures of N2O. It was validated for field conditions application and can provide quantification of N2O reduction also providing uncertainity assessment.
We appreciate reference to this study. We will suggest including the 3 isotopes of N2O for future developments of the model in the revised manuscript.
L250 tests were included
Thank you, we will fix this grammatical error.
L269 you need to define how eta values are defined and which values you applied for them Table 1 – there is new review paper by Yu et al, 2020 (RCM 34 (20): e8858, appendix) summarising the values, it would be most up to date to cite these (there are some important changes in the ranges)
We will rerun the analyses with the newest end members and eta values summarized in Yu et al. 2020 and include appropriate definitions in the revised manuscript. We do not expect the model outcomes to change drastically, based on our evaluation of the impact of uncertainty around the isotope endmembers on model predictions.
L 286 you say that there is a common range for nitrification and fungal denitrification – in the most recent review (Yu et al., 2020) it has been shown that the d18O for nitrification should be slightly different than assumed in previous publications, you should either decide which of these processes is more relevant for your study or assume a slightly wider range for d18O
Thank you for the suggestion, we will change the revised manuscript accordingly.
Eq 7,8 – eta*F reduced/diffused – you make open system assumption in your equations – definitely right for diffusion, but can be doubt for N2O reduction, there might be values which cannot be explained with open system equation (Lewicka-Szczebak et al., 2014, 2017), or you can wrongly attribute this to larger proportion of nitrification. Especially given that you have large reduction it makes big difference if using open or closed system equations. I would check what is the difference and report this. You have only justified using the open system equation with the argument of simplified maths, but I think this generates significant bias. The requirement for using open system equation is the equilibrium of the fluxes in and out (Fry, 2006) and you clearly do not have this between N2O production and reduction.
We acknowledge that carefully considering open versus closed system dynamics is important. If N2O production and reduction occur simultaneously, both open or closed dynamics could occur. The reviewer refers to the requirement of equilibrium between the fluxes in and out for open system dynamics, and argues this is not the case in our study. We kindly disagree with this assessment. Given the slow but steady change of N2O and isotope values over time observed in our study, fluxes in and out may well be at near equilibrium in distinct time points. In the study by Lewicka-Szczebak and collegues (2017), instantaneous N2O emitted from the soil surface was measured during an incubation, where a N2O pulse was observed following application of fertilizer N. When plotting isotope values of N2O in function of the residual N2O fraction, a logarithmic fit was found, which could be described by the Rayleigh equation that describes N2O fractionation under closed system dynamics. This clearly illustrates that in their study, closed system dynamics prevailed during N2O reduction. It should be noted, however, that the patterns observed in Lewicka-Szczebak et al. (2017) are only expected to occur if N2O source processes remain constant, while there is a progressive reduction of N2O over time. If N2O production from nitrification increase or decrease over time, very different patterns would have emerged. The figures below show simulated relationships between SP of the instantaneous product and the residual substrate fraction under scenarios where N2O production is constant over time, vs. where N2O production from nitrification and denitrification changes over time, for open vs. closed system dynamics. In all scenarios, we assumed that the residual fraction of N2O decreases progressively over time (see figure in attached supplement).
We argue that, while the study by Lewicka-Szczebak et al. (2017) marked an important milestone in furthering how to interpret N2O isotope values, the study does not provide unequivocal evidence that closed system dynamics will prevail in all scenarios where N2O production and reduction occur simultaneously. This leaves the question, when is it appropriate to use open vs. closed system dynamics? In a simulation by Denk et al. 2017, it was shown that the difference between open and closed system dynamics becomes small at small time steps, even when the fraction of residual substrate becomes very small. Given that closed system dynamics would lead to a system of complex non-linear equations that are much harder to solve numerically, we opted to use open system dynamics and a small time step. We will elaborate on this point in the discussion, including recommendations for future research to provide more clarity on this issue.
Denk, T. R. A., et al. (2017). "The nitrogen cycle: A review of isotope effects and isotope modeling approaches." Soil Biology & Biochemistry 105: 121-137. (Fig. 7)
Did you take into account atmospheric N2O diffusing into the soil? Have you sampled ambient air for N2O isotopic analyses?
Ambient air samples were taken and analyzed for N2O concentrations as well as isotope values of N2O. The model does calculate diffusion between the ambient air and the 0-7 cm depth increment. A positive value would indicate a net flux out of the soil, a negative value a net flux into the soil.
L 555 (Appendix) – “With various terms cancelling out, the equation can be rewritten as:” – why can you cancel out “various things”, what are these “various things” and how this cancelling out influences the final result?
Please see answer in attached document. We were not able to insert equations in the easily in the comment post box.
L563 (Appendix) – “For approaching 0, the equation can be further simplified as:” – why can you assume Dt approaching 0? It is one day, right? When you are using fluxes in your equations you need the time factor to be included in the equations, I guess. What are the units for the fluxes used in your Eq 7 and 8?
Please see answer in attached document. We were not able to insert equations in the easily in the comment post box.
Table 3 You have given the N2O fluxes without time units. For which time period are the amounts given (per hour, per day?) Table 5 – same as above
The values are cumulative N2O production and consumption rates over the experimental period, which was approximately 5 months. We will add this information in the table captions.
L355-357 – I am not sure if Fig 1 really supports this statement. For some isotopic signatures you have really large variations within the 2 weeks time, eg. SP values 7.5cm depth
The reviewer refers to the statement “Similarly, subsurface isotope values of N2O showed a relatively consistent temporal pattern (Fig. 1). The temporal patterns in subsurface N2O concentrations and isotope concentrations observed in this and other studies (van Groenigen 2005, Verhoeven 2019) suggest that a sampling frequency of once every two weeks or once a month may be sufficient to adequately capture subsurface N2O dynamics.” While we agree with the reviewer that some of the variation in isotope values between sampling points is relatively high, we argue that there is a clear and strong pattern of increasing isotope values over the course of the experimental period, that appears stronger than the variations between reps and sampling points that are closer together in time (See Fig. 1).
L361 – very low SP – cannot be explained with any known literature data?! Can this be due to some measurement or evaluation problem? As these are individual samples you should carefully look on their measurements – was the N2O concentration in good range? Check your normalisation procedure for evaluation of SP data. What is your lowest SP standard? If your lowest standard value is near atmospheric air (eg. +18) then your normalisation for such low values may produce large offset (see Mohn et al, 2014).
IRMS calibration was done with two isotopically different standards (see Verhoeven 2019). We did not omit any data which had passed our internal quality check. However, a small fraction of the samples was analyzed before we implemented an activated charcoal trap. This trap was implemented in our inlet system as we observed strong mass interferences from unknown sources. We speculate that especially soil pore gas samples can potentially be contaminated with VOCs or other gaseous compounds interfering with the measurement. The very low SP values stem from the period when measuring without an activated charcoal trap. N2O concentrations were generally in a good range. Our lowest SP standard is at -1.62 permil.
You also have d15N data, why not using them in the modelling as well? Maybe then can be useful in distinguishing further processes like nitrification and fungal denitrification (in case you would also analyse the substrates).
We appreciate the reviewer’s suggestion. Values of δ15N-N2O are impacted by the δ15N of the substrate, which can change rapidly and strongly over time (Decock and Six, 2013). In the absence of data on δ15N of the substrate, we did not feel confident including δ15N as a constraint. However, expanding the model to include δ15N data may be a great opportunity for future developments.
Fig 3b, 3c – why there are no error bars for the points before day20 and after day100?
The error bars are so small that they can’t be seen on the figure.
Section 2 – have you analysed d18O of soil water? If so, please describe, which method, how many samples etc. If not, please justify your assumption on -9.9 permil.
The δ18O value measured for tapwater at the facility was used in this study. The value is actually -11 permil. We accidentally copied the wrong value over from Verhoeven et al. 2019 in the footnote under table 1. We will correct this in the revised manuscript and add details on the method to measure δ18O in tapwater in the materials and methods section. We will also elaborate in the discussion on how time and depth differentiated measurements of soil water δ18O are recommended for field studies.
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AC1: 'Reply on RC1', Charlotte Decock, 14 Mar 2023
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CC1: 'Comment on bg-2022-221', Reinhard Well, 05 Jan 2023
Comment by Reinhard Well, Thuenen-Institute, Braunschweig, Germany
The attempt to use soil air N2O isotopes to constrain N2O processes is timely in view of many data reports lacking conceptual or physical models to interpret results. Therefore the presented approach is really needed and very promising from my view. In view of the close deadline of open discussion I could not find time to look at this interesting paper in detail, unfortunately, but just went briefly through methods and key results. I am impressed by the very nice lysimeter study yielding a very valuable data-set as far as I can see.
With regard to interpretation and calculations I came across the following points that might be subject to further consideration:
- The magnitude of calculated denitrification rates of up to > 100 kg N/ha in about 5 month is quite high for terrestrial mineral soils. I would not say impossible but quite astonishing. Total N2o fluxes are, however, in typical range, giving N2O/(N2O+N2) ratios about 1-2%, eg much lower compared to most previous reports. Still not impossible, but astonishing, maybe due to high pH and/or low diffusivity? The estimated N2O production from nitrification (N2Onit), however, is impossible from my view. It is well known that the N2O yield of nitrification is always very small with values around 0.1% typical and rarely above 1% (e.g. Hink, L., et al. (2017). "Archaea produce lower yields of N2O than bacteria during aerobic ammonia oxidation in soil." Environmental Microbiology 19(12): 4829-4837. But you report N2Onit up to 25 kg/5 month. Assuming a very high N2O yield of nitrification of 1% this would mean gross nitrification was 2500 kg N/ha/5 month. I think this is far beyond all previous reports in soils.
- What could be the reason for possible overestimating N2O production and consumption? I think it could be the fact that you assume open system dynamics for isotopic fractionation during N2o reduction. I recall we had a discussion on this after the Decock & Six review in 2013 and my impression was that later on most authors assumed that closed system dynamics are more probable for soil denitrification. In the study of Lewicka-Szczebak, D., et al. (2017). "Quantifying N2O reduction to N2 based on N2O isotopocules – validation with independent methods (helium incubation and 15N gas flux method)." Biogeosciences 14(3): 711-732. this could be confirmed by independent measurement of N2 fluxes, since a match of NA isotopes and 15N-tracing was only obtained when assuming closed system dynamics. To illustrate the huge difference in calculated N2O reduction when using closed or open system dynamics one might use the equations for closed and open system fractionation shown in in Decock and Six 2013 and calculate SP using the unreduced fraction of N2O (f) of e.g 0.02 according to Monte Calme treatment in Table 5, giving for open system: SP = SP0 - εSP (1 - f) = -2.4permil - (-5.3permil) * (1-0.02) = 2.8 per mil; for closed system: SP = SP0 + εSP * ln(f) = -2.4permil + (-5.3permil) * ln(0.02) = 18.3 permil. So this shows the huge difference of both approaches for small f values, while results are more similar for f values close to 1. Looking at the SP value of open system dynamics yielding f = 0.02 we can check which f value would be obtained by closed system dynamics if we solve the equation for f giving: f = exp((SP-SP0)/eSP) = 0.38. This shows that closed system would lead to much higher N2O/(N2+N2O ) ratios.
- Strong overestimation of N2O reduction due to open system assumption would also explain the very high N2Onit values: if the combination of SP and d18O values yields a fraction from nitrification of say 30%, then with the large values of total N2O consumption you end up with these high numbers for N2Onit. So possibly, by assuming closed system dynamics you would solve this contradiction.
- Some more detailed discussion how N2O consumption could be larger than production would be helpful.
- I was astonished about another number: bulk density of > 1.7 after sieving and packing. How in the world did you achieve this with sieved loamy soil? I think it is only possible with extreme compaction and I wonder how wheat could grow. If you used indeed extreme compaction procedure then you might report why you chose this and how it was achieved. With BD about 1.7, diffusivity must have been extremely low during moist phases and thus could indeed explain extreme denitrification rates. I think the paper would gain if you discussed the uncertainty from calculated diffusivity and assuming constant BD. You might also consider that for low air filled porosity (as maybe in your case ) there are special equations for Ds (eg Sallam, A., et al. (1984). "Measurement of Gas Diffusion Coefficient under Relatively Low Air-filled Porosity." Soil Science Society of America Journal 48(1): 3-6)
But irrespective of the question whether my concerns are justified or not, I think your approach is really promising. Would be nice if someone would check its outcome using independent methods soon. I always found this very helpful when evaluating new denitrification methods.
Citation: https://doi.org/10.5194/bg-2022-221-CC1 -
AC2: 'Reply on CC1', Charlotte Decock, 14 Mar 2023
We thank the reviewers for their constructive and thorough comments. Please find reviewer comments followed by author response to each column below. Author responses are shown in bold.
Comment by Reinhard Well, Thuenen-Institute, Braunschweig, Germany
The attempt to use soil air N2O isotopes to constrain N2O processes is timely in view of many data reports lacking conceptual or physical models to interpret results. Therefore the presented approach is really needed and very promising from my view. In view of the close deadline of open discussion I could not find time to look at this interesting paper in detail, unfortunately, but just went briefly through methods and key results. I am impressed by the very nice lysimeter study yielding a very valuable data-set as far as I can see.
We thank the reviewer for this kind and encouraging evaluation of our work.
With regard to interpretation and calculations I came across the following points that might be subject to further consideration:
The magnitude of calculated denitrification rates of up to > 100 kg N/ha in about 5 month is quite high for terrestrial mineral soils. I would not say impossible but quite astonishing. Total N2o fluxes are, however, in typical range, giving N2O/(N2O+N2) ratios about 1-2%, eg much lower compared to most previous reports. Still not impossible, but astonishing, maybe due to high pH and/or low diffusivity?
We agree with the reviewer that total denitrification rates are high but within range of what has been observed in the literature. We provide an extensive discussion on potential explanations in the manuscript, including limitations of alternative methods to estimate total denitrification.
The estimated N2O production from nitrification (N2Onit), however, is impossible from my view. It is well known that the N2O yield of nitrification is always very small with values around 0.1% typical and rarely above 1% (e.g. Hink, L., et al. (2017). "Archaea produce lower yields of N2O than bacteria during aerobic ammonia oxidation in soil."Environmental Microbiology 19(12): 4829-4837. But you report N2Onit up to 25 kg/5 month. Assuming a very high N2O yield of nitrification of 1% this would mean gross nitrification was 2500 kg N/ha/5 month. I think this is far beyond all previous reports in soils.
We appreciate the back-of-the envelope calculations provided here and feel it is a great way to evaluate if the rate constraints by our model are realistic or not. We do not think, however, that a gross nitrification rate of 2500 kg N/ha/5 months is unrealistic. Gross nitrification rates in agricultural soil have been found to range between 0.2 and 10 mg N kg soil-1 day-1(Booth et al., 2005). Assuming a rate of 5 mg N kg soil-1 day-1 and 2,000,000 kg soil in a 15 cm depth increment, this would come down to 1500 kg N ha-1 over 150 days. Hence, when considering a soil profile of 150 cm, 2500 kg N/ha/5months is not so unreasonable anymore.
What could be the reason for possible overestimating N2O production and consumption? I think it could be the fact that you assume open system dynamics for isotopic fractionation during N2o reduction. I recall we had a discussion on this after the Decock & Six review in 2013 and my impression was that later on most authors assumed that closed system dynamics are more probable for soil denitrification. In the study of Lewicka-Szczebak, D., et al. (2017). "Quantifying N2O reduction to N2 based on N2O isotopocules – validation with independent methods (helium incubation and 15N gas flux method)." Biogeosciences 14(3): 711-732. this could be confirmed by independent measurement of N2 fluxes, since a match of NA isotopes and 15N-tracing was only obtained when assuming closed system dynamics. To illustrate the huge difference in calculated N2O reduction when using closed or open system dynamics one might use the equations for closed and open system fractionation shown in in Decock and Six 2013 and calculate SP using the unreduced fraction of N2O (f) of e.g 0.02 according to Monte Calme treatment in Table 5, giving for open system: SP = SP0 - εSP (1 - f) = -2.4permil - (-5.3permil) * (1-0.02) = 2.8 per mil; for closed system: SP = SP0 + εSP * ln(f) = -2.4permil + (-5.3permil) * ln(0.02) = 18.3 permil. So this shows the huge difference of both approaches for small f values, while results are more similar for f values close to 1. Looking at the SP value of open system dynamics yielding f = 0.02 we can check which f value would be obtained by closed system dynamics if we solve the equation for f giving: f = exp((SP-SP0)/eSP) = 0.38. This shows that closed system would lead to much higher N2O/(N2+N2O ) ratios. Strong overestimation of N2O reduction due to open system assumption would also explain the very high N2Onit values: if the combination of SP and d18O values yields a fraction from nitrification of say 30%, then with the large values of total N2O consumption you end up with these high numbers for N2Onit. So possibly, by assuming closed system dynamics you would solve this contradiction.
We appreciate the reviewer’s reflection, but kindly disagree that there is evidence for N2O production and consumption to be overestimated in our study. While there is no true validation of our model results, we argue in the discussion section of the manuscript and responses to other comments that our findings are well within the roam of what has been found in the literature. We do acknowledge, however, that this is a proof-of-concept study and future research should continue to improve and validate our proposed modeling approach. We also fully agree that the issue of open vs. closed system dynamics needs to be addressed, and provided details on how this will be addressed in the revised manuscript in responses to other comments.
Some more detailed discussion how N2O consumption could be larger than production would be helpful.
We refer the reviewer to responses to comments posed by other reviewers. We will edit the revised manuscript accordingly.
I was astonished about another number: bulk density of > 1.7 after sieving and packing. How in the world did you achieve this with sieved loamy soil? I think it is only possible with extreme compaction and I wonder how wheat could grow. If you used indeed extreme compaction procedure then you might report why you chose this and how it was achieved. With BD about 1.7, diffusivity must have been extremely low during moist phases and thus could indeed explain extreme denitrification rates. I think the paper would gain if you discussed the uncertainty from calculated diffusivity and assuming constant BD. You might also consider that for low air filled porosity (as maybe in your case ) there are special equations for Ds (eg Sallam, A., et al. (1984). "Measurement of Gas Diffusion Coefficient under Relatively Low Air-filled Porosity." Soil Science Society of America Journal 48(1): 3-6)
We acknowledge that the bulk density measured in our lysimeters is very high. We triple checked our calculations and noted that the bag weight had not been subtracted. After this correction, the bulk density was still relatively high at 1.64 g/cm3. As discussed in our response to another comment, the high bulk density is likely due to settling and compaction of the soil over the 7-month period, where repeated watering may have caused slaking and compaction. The bulk density may also have been inflated by the measurement procedure, using a sliding hammer core to take soil samples. We recognize the importance of a good bulk density estimate for diffusion modeling. Given that this is a proof-of-concept study, we plan to rerun the model with the updated bulk density value and do a sensitivity analysis on how the model outcomes respond to bulk density in the revised manuscript.
But irrespective of the question whether my concerns are justified or not, I think your approach is really promising. Would be nice if someone would check its outcome using independent methods soon. I always found this very helpful when evaluating new denitrification methods.
We fully agree with the reviewer. We underline that his is a proof-of-concept study and hope our work will inspire future research in this field. There are many opportunities for further model development. We will highlight that in the revised manuscript.
References
Booth, M.S., Stark, J.M., Rastetter, E., 2005. Controls on nitrogen cycling in terrestrial ecosystems: A synthetic analysis of literature data. Ecological Monographs 75, 139-157.
Decock, C., Six, J., 2013. An assessment of N-cycling and sources of N2O during a simulated rain event using natural abundance 15N. Agriculture, Ecosystems & Environment 165, 141-150.
Citation: https://doi.org/10.5194/bg-2022-221-AC2
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RC2: 'Comment on bg-2022-221', Anonymous Referee #2, 11 Jan 2023
The manuscript bg-2022-221 reports on a model concept to calculate total denitrification based on natural abundance N2O isotopic composition. This is an extremely important subject that has remained a challenge especially due to the complications in measuring N2 emissions. From this perspective, this study is an important contribution for the scientific community, is well placed in a journal like BG and in my opinion definitely deserves publication.
The study is extremely well structured and written, so that formal comments hardly arise. However, there are some aspects that need to be considered:
- The presentation of available data is not complete. Soil-atmosphere flux rates of N2O were determined using static chambers, but the time series of N2O emission is not shown and only used to calculate cumulative emission. Are there any emission peaks after fertilizer applications? Is there an emission event between day 80 and 100 when soil N2O concentration shows a peak (Figure 2a)? Diffusion fluxes for the top of soil compartment 1 could be easily (and should be) plotted together with measured N2O emissions. Time series of the production/consumption rates in the various depths would also be informative. Fertilizer application dates are not shown in figures, which is a pity.
- A major point is that N2O consumption is consistently larger than N2O production. Does this mean that layer 1 takes up N2O? From this perspective, it appears quite nonrational to not assess the influence of constraining the model with an alternative upper boundary condition. At the moment, a constant concentration boundary is applied at the upper end of the soil profile. I ask the authors to use a flux boundary at the top of layer 1 and investigate in how far this procedure changes results. Additionally, a sensitivity analysis could hep to find a parameter set that allows for N2O emissions while estimating sound N2O production rates
- I am not sure if the concept of smooth functions is really adequate. N2O production in soil, and, thus N2O emission is notorious for its episodic behaviour. From this perspective, short-term increase in soil air N2O concentrations will be associated with flux events. Using smooth functions will suppress all short-term behaviour as these events are neglected by smoothing algorithms. This also refers to figure 2a (see point 1), which is obviously suppressed by the smooth functions. àAfter having read the manuscript again, I am not even sure if I understand what the authors mean exactly with smooth functions. In the first moment I thought the aim was to fit a function that is analytically differentiable. But I have the impression that the derivatives were formed numerically? Please clarify.
- Maybe the most important point is that the state equations are not unconditionally physically sound. For instance, the mixing term in equations 7 and 8 is not constrained mathematically. Just consider a situation in which N2Onit is four times larger than the stored N2O concentration and SP0 is 0. Then the shift in SP would be something like 120 per mil which is impossible as the shift has to be limited to SPnit-SP0. I am aware that the authors have derived this simplification under the assumption that Dtà0, but this is not forced in the numerics. This means that a time step control function / criterion needs to be defined. Or the independence of the solution of Dt needs to be shown (plot of solutions for different Dt).
- There is no validation data for the model at all. The only available information is N2O flux rate. N2O flux rates show emission of N2O from the soil while the model result suggests constant? N2O consumption. In absence of other validation parameters, the message that the model produces reasonable results is not convincing. What parameter changes are necessary to obtain N2O emission from the top layer and what conclusions for the model concept follow from this?
Please find details below.
Title
ok
Highlights
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Abstract
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Introduction
Materials and Methods
L135: Please check bulk density value. It is a quite high value and rather unlikely to result from repacking unless massive pressure was applied during the process.
L209: Not using available surface fluxes seems nonrational to me. It is a direct constraint and could be used directly for the later described equations 6, 7 and 8 for the top layer.
L208: please clarify what semi-independent means in this context.
L214-216: was the system of linear equations formulated in a way that there is one system per layer or was there one system for all layers combined?
L223: It may be pertinent to add that concentration C is in volume per volume, i.e., m3 m-3?
L225: please check value. It is quite impossible that a greenhouse is able to maintain a mixing ratio so much lower than atmospheric mixing ratio. Or is this an uncalibrated raw reading?
Section 2.5.3: I have some problems with the smooth functions. I think I perfectly understand why the authors have chosen smooth functions, since they are unconditionally differentiable at any point in time, however, isn’t the essence of N2O emission its notoriously episodic character? And can this episodic character be reproduced by smooth functions? In view of Figure 2a, I think that important aspects like a possible emission peak between day 80 and 100 could have been overlooked by selecting smooth functions.
L248-254: This paragraph is rather incomprehensible: What does “All data values are averaged at each time step of measurements and then indexed by time” mean? If measurements are 8 hours apart from each other and equidistant, were measurement time +- 4 hours averaged? Or do the authors refer to the replicate lysimeters?
Was the most suitable smoothing function the one with the lowest sum of square error of fit?
Please explain time series bootstrapping. I don’t see how the uncertainty of the transient N2O concentration in a layer can be obtained by time series bootstrapping.
Equations (8) and (9): These equations are used to reflect both isotopic fractionation and mixing. However, the mixing part is necessarily mass / isotope conserving. I.e., it is only a valid approximation if Ftop, Fbot, N2Onit, N2Oden and N2Ored are small compared to N2Oconc,0. The reason is as follows: Assume that in (7), N2Onit 4 times N2Oconc,0 and SP0 is 0. The shift in SP would be 4 *34.4 per mil = 137.6 per mil. This is outright impossible. Consequently, the formulation as it is doesn’t ensure a physically sane mixing process as the highest possible shift would be limited to a shift that results in SP of 34.4 per mil for nitrification-derived N2O and 0 for denitrification. This means, the authors need to find criterions for the time step control or find a formulation that allows simultaneous fractionation and mixing calculations in a mathematically correct way.
L284: diffusion isotope effects have different sign and massively different magnitude. How can the isotope effect of diffusion be so different if the mass difference between 14N15N16O and 14N14N18O is only in the range of 1/46 ~ 2.1%? Considering the low inverse isotope effect of diffusion for SP and the inverse sign of d18O, I am wondering if these isotope effects are robust.
L310-313: I fully agree that at small time steps, open and closed system calculations yield the same results. However, the adequate time step size depends on magnitudes of flux rates, N2O concentration and isotope effect. The authors have to at least show that results did not change significantly for different time steps or present a time step control.
Results
L339: 0 to 30 ppm is a huge range. Were there amount effects, i.e., an effect of N2O mixing ratio on isotopic composition? Was this checked in any way? Please refer to it in your methods section.
L348: please change second “where” to “were”.
L352-354: it actually seems like a stark contrast to pulse emissions, but in the paper, I could not find soil-atmosphere N2O flux. Could you please provide the time series of the chamber flux measurements and integrate it in the publication?
L400: The uncertainty analysis is important, and very much appreciated. However, I am confused when looking at Figure 3. It seems like all variations in endmembers and input variables will result in lower production or consumption rates when rates are higher than 0.3 kg ha-1 day-1. Please explain this behavior. I assumed to see both positive and negative deviations. Is the used parameter set some unique constellation of values?
At lower rates, the model doesn’t seem robust (see values after day 100) at which relative deviation of fitted rates are massive. This needs to be discussed.
Discussion
L460-462: whether or not soils are net sinks or sources for N2O is a fundamentally important question. The model results of net N2O uptake from the atmosphere contradict the observation of typical N2O emission rates. At this point, the authors need to further investigate possible reasons. One striking aspect is already shown in Figure 3: Nitrification- and denitrification-related N2O emissions were lower if uncertainty in endmembers or input variables (bulk density, soil moisture, N2O concentrations and isotopic composition) was considered. This may indicate that different endmembers or input parameters may decrease the discrepancy of gross production and consumption. The model should for sure be constrained in a way that the surface fluxes are reproduced by the model.
In addition, the figures lack indication of fertilizer application. Was fertilizer application associated with soil-atmosphere fluxes?
L497-499: Decoupling is one possibility, but alternatively, N2O production pulses in a top soil layer may be concealed due to the low sampling rate. This may be a consequence of the shorter travelling time of a N2O molecule that is produced close to the soil-atmosphere boundary. Higher soil moisture at lower depths may decrease transport rates out of the soil.
Conclusion
L527-528: I don’t agree that your model has necessarily constrained total denitrification, especially since total soil-atmosphere exchange could not be reflected. Your study has definitely shown that N2O production needs to be largely balanced by consuming processes. But you could not show in how far the solutions are accurate with regard to magnitude of fluxes.
Supporting information
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Citation: https://doi.org/10.5194/bg-2022-221-RC2 -
AC3: 'Reply on RC2', Charlotte Decock, 14 Mar 2023
We thank the reviewers for their constructive and thorough comments. Please find reviewer comments followed by author response to each column below. Author responses are shown in bold.
The manuscript bg-2022-221 reports on a model concept to calculate total denitrification based on natural abundance N2O isotopic composition. This is an extremely important subject that has remained a challenge especially due to the complications in measuring N2 emissions. From this perspective, this study is an important contribution for the scientific community, is well placed in a journal like BG and in my opinion definitely deserves publication.
The study is extremely well structured and written, so that formal comments hardly arise. However, there are some aspects that need to be considered:
The presentation of available data is not complete. Soil-atmosphere flux rates of N2O were determined using static chambers, but the time series of N2O emission is not shown and only used to calculate cumulative emission. Are there any emission peaks after fertilizer applications? Is there an emission event between day 80 and 100 when soil N2O concentration shows a peak (Figure 2a)? Diffusion fluxes for the top of soil compartment 1 could be easily (and should be) plotted together with measured N2O emissions. Time series of the production/consumption rates in the various depths would also be informative. Fertilizer application dates are not shown in figures, which is a pity.
We appreciate the reviewer’s recognition of the richness of the dataset. The paper already has 5 figures and 5 tables, so we opted not to show time series of N2O production and consumption for each treatment and depth increment. Likewise, we opted not to include a comparison of the diffusion fluxes for the surface layer and daily N2O surface fluxes measured using the closed chamber technique, as it is not the major focus of the study. Several previous studies have made such comparisons, and generally conclude that there are discrepancies between the methods. Likely, the diffusion gradient method is unable to assess N2O dynamics in the very top few cm of the soil. We acknowledge, however, that providing the additional data may be valuable to the community and will provide the additional charts in supporting information in the revised manuscript. In addition, we will provide an R markup file with the core of the code and a file with the raw N2O concentrations and isotope values of N2O at each depth for each lysimeter over the course of the experimental period. This can support further advancement of models concerned with N2O dynamics in the soil profile.
A major point is that N2O consumption is consistently larger than N2O production. Does this mean that layer 1 takes up N2O?
N2O consumption is consistently larger than N2O production because the N2O concentration in the soil profile at the start of the experiment is greater than the N2O concentration in the soil profile at the end in the lower 3 depth increments. Potentially, N2O built up prior to the start of the experiment as soil was repacked and wetted, followed by a slow net consumption over the course of the experiment. Note that the difference between N2O production and consumption is relatively small and not significant when considering variation across replicates. It should be noted that N2O flux rates are generally 1000 times smaller than other gross N transformation rates in the N cycle. Our study suggest that gross N2O production and consumption rates may be more in the range of other gross N transformation rates, which exemplifies why it is so hard to accurately measure N2O surface fluxes. We acknowledge that future model development may reduce uncertainty and add additional constraints to the model to address this issue.
From this perspective, it appears quite nonrational to not assess the influence of constraining the model with an alternative upper boundary condition. At the moment, a constant concentration boundary is applied at the upper end of the soil profile. I ask the authors to use a flux boundary at the top of layer 1 and investigate in how far this procedure changes results.
We thank the reviewer for this suggestion. Given that this analysis would add a significant amount of work, we suggest this would be a great subject for future research. We will make note of this suggestion in a section on recommendations for future developments in the revised manuscript.
Additionally, a sensitivity analysis could hep to find a parameter set that allows for N2O emissions while estimating sound N2O production rates
We do not believe our gross N2O production rates are unsound. Likely, the challenge lies in gross N2O production and consumption rates being effectively orders of magnitude greater than net N2O surface fluxes, complicating model development for good estimations of both gross N2 loss and N2O surface emissions. Future model development should focus on this issue.
I am not sure if the concept of smooth functions is really adequate. N2O production in soil, and, thus N2O emission is notorious for its episodic behaviour. From this perspective, short-term increase in soil air N2O concentrations will be associated with flux events. Using smooth functions will suppress all short-term behaviour as these events are neglected by smoothing algorithms. This also refers to figure 2a (see point 1), which is obviously suppressed by the smooth functions. After having read the manuscript again, I am not even sure if I understand what the authors mean exactly with smooth functions. In the first moment I thought the aim was to fit a function that is analytically differentiable. But I have the impression that the derivatives were formed numerically? Please clarify.
We agree with the reviewer that surface N2O fluxes are notorious for their high temporal and spatial variability leading to hot moments and hotspots. To date, however, studies that have measured subsurface N2O concentrations have not observed this type of behavior. In addition, the goal of the study is not to accurately estimate the temporal variability in N2O surface emissions, but to estimate gross N2 loss over the soil profile. In this context, we believe fitting a smooth curve to the data is appropriate. The current fits to the subsurface data include a linear model, a cubic spline, and a loess function. To determine derivatives, we calculated the slope to the fitted curve for discrete time points. Future model development will focus on developing smooth curves capable of more closely capturing temporal variation in the data, for example by using different versions of Gaussian processes to smooth measurements or source contributions directly.
Maybe the most important point is that the state equations are not unconditionally physically sound. For instance, the mixing term in equations 7 and 8 is not constrained mathematically. Just consider a situation in which N2Onit is four times larger than the stored N2O concentration and SP0 is 0. Then the shift in SP would be something like 120 per mil which is impossible as the shift has to be limited to SPnit-SP0. I am aware that the authors have derived this simplification under the assumption that Dtà0, but this is not forced in the numerics. This means that a time step control function/criterion needs to be defined. Or the independence of the solution of Dt needs to be shown (plot of solutions for different Dt).
Thank you for this comment. We would like to emphasize that the model is not meant to be a simulation model. We do not aim to estimate the shift in isotope values over time by parameterizing process rates. Instead, we discretize time series of patterns in N2O concentrations and isotope values to estimate N2O production and consumption rates at each time point. Thus, the rates are nearly independently estimated at each time point based on observed patterns in N2O concentrations and isotope values, along with isotope end-members for N2O production and consumption processes characterized in the literature. Our model has 3 unknowns, namely gross N2O production by nitrification, gross N2O production by denitrification, and gross N2O consumption, and 3 equations. A solution for the system of equations is sought at each time point. We acknowledge that including more source processes or isotopic constraints may improve the model in future iterations, but this is outside of the scope of the current study.
There is no validation data for the model at all. The only available information is N2O flux rate. N2O flux rates show emission of N2O from the soil while the model result suggests constant? N2O consumption. In absence of other validation parameters, the message that the model produces reasonable results is not convincing. What parameter changes are necessary to obtain N2O emission from the top layer and what conclusions for the model concept follow from this?
We acknowledge that there is no true validation of the model results. However, no method currently exists that adequately estimates gross N2O production in the soil profile, rendering a true validation impossible. As discussed in the manuscript, all methods have their flaws, and we know quite little about gross N2 production rates. Studies targeting denitrifier genes in the soil profile consistently find high abundances, suggesting denitrification is indeed ubiquitous in the soil. In our discussion, we invite the readers to open their minds to the idea that total denitrification, in some soils, may be greater than previously thought. It should be emphasized that our model is a proof-of-concept study. In future studies, it would be valuable to compare gross N2 production rates based on this approach with other methods, particularly compared to 15N tracers methods and direct N2 quantification under low N2 atmosphere. We also note that the model does not aim to estimate surface N2O fluxes based on subsurface N2O dynamics. In contrast, the main aim of our approach is to estimate total N2 loss. In this context, we argue that gross N2O production and consumption rates likely operate at a different order of magnitude compared to surface fluxes, possibly shedding some light on why accurately measuring and simulating surface N2O emissions has been so challenging.
Please find details below.
Materials and Methods
L135: Please check bulk density value. It is a quite high value and rather unlikely to result from repacking unless massive pressure was applied during the process.
We agree with the reviewer that the bulk density measured in our experiment is quite high. It should be noted that the experiment was set up in 1.5m tall and 0.5 m diameter lysimeters. The repacked soil was watered and allowed to settle and equilibrate for two months before the start of the experiment. It is possible that heavy disturbance of soil during repacking followed by sequential deep waterings of the lysimeters caused slaking of aggregates and compaction. Furthermore, bulk density was assessed at the end of the experiment, at which point the soil had been in the lysimeters for 7 months. During destructive sampling, a sliding hammer soil core was used the collect ‘undisturbed’ soil cores with known volume. Some additional compaction may have happened during the sampling procedure. The soil felt notable compacted during destructive sampling. Finally, the soil has a relatively high sand content (58%) and low soil organic carbon (0.08% in topsoil and 0.04% in subsoil), both of which generally results in higher bulk density.
L209: Not using available surface fluxes seems nonrational to me. It is a direct constraint and could be used directly for the later described equations 6, 7 and 8 for the top layer.
We appreciate the suggestion but given the well documented mismatch between surface fluxes and fluxes based on the gradient method, we do not believe this is a good approach for estimating gross N2 production in the soil profile. The commonly observed mismatch between N2O surface fluxes based on the gradient method and flux chamber measurements suggests at least a partial decoupling of N2O dynamics in the very top few cm of soil relative to the rest of the profile. Given that the focus of this study is to constrain N2 production in the soil profile, we do not believe that surface fluxes would help in constraining the model.
L208: please clarify what semi-independent means in this context.
We mean that the only relationship between two time points is the smooth curve. The smooth curve aims to fit the pattern in the data over time as well as possible without making assumptions about underlying mechanisms or reaction kinetics. Its only purpose is to be able to estimate the infinitesimal change in the concentration or isotope value at each time point, using the first derivative. The gross N2O production and reduction rates are estimated separately for each time point and depth increment. Therefore, we consider the estimates at each time point semi-independent. We will specify this accordingly in the revised manuscript.
L214-216: was the system of linear equations formulated in a way that there is one system per layer or was there one system for all layers combined?
There was one system per layer. We will specify this accordingly in the revised manuscript.
L223: It may be pertinent to add that concentration C is in volume per volume, i.e., m3 m-3?
Thank you for this suggestion, we will implement the change accordingly in the revised manuscript.
L225: please check value. It is quite impossible that a greenhouse is able to maintain a mixing ratio so much lower than atmospheric mixing ratio. Or is this an uncalibrated raw reading?
This was an uncalibrated raw reading. We are sorry for this oversight and will make necessary edits to the manuscript.
Section 2.5.3: I have some problems with the smooth functions. I think I perfectly understand why the authors have chosen smooth functions, since they are unconditionally differentiable at any point in time, however, isn’t the essence of N2O emission its notoriously episodic character? And can this episodic character be reproduced by smooth functions? In view of Figure 2a, I think that important aspects like a possible emission peak between day 80 and 100 could have been overlooked by selecting smooth functions.
The reviewer is correct in guessing that our choice for the smooth functions is that they are unconditionally differentiable at any point in time. As noted earlier, we agree that N2O is notoriously temporal variable when it comes to surface fluxes, but N2O subsurface concentrations published to date do not seem to follow the same trend. Patterns in subsurface N2O concentrations tend to change much more slowly over time. In our data set, there is one exception, in the 7.5 cm depth layer in one of the lysimeters. We argue that this one observation may be an outlier.
L248-254: This paragraph is rather incomprehensible: What does “All data values are averaged at each time step of measurements and then indexed by time” mean? If measurements are 8 hours apart from each other and equidistant, were measurement time +- 4 hours averaged? Or do the authors refer to the replicate lysimeters?
We thank the reviewer for pointing out the ambiguity in this phrasing and will edit as needed in the revised manuscript. Diffusion fluxes are calculated based on the observed N2O concentrations at each time point of observation. This was done for each lysimeter and each depth increment individually. Then, smooth functions were fit for each depth and lysimeter for diffusion fluxes, N2O concentrations, and isotope values. Smooth functions were indexed by time on a daily time step over the course of the experimental period, and derivatives and predicted values were determined for each day. As such, the system of equations was solved for each day, while original data was collected on a weekly basis, but the smooth functions interpolated between measurements days. We hope this clarification helps.
Was the most suitable smoothing function the one with the lowest sum of square error of ifit?
If the loess or base spline fit were not significantly different from the linear model, a linear fit was assumed. Choice between base spline and loess fit was based on visual observations of how well the predicted data fit the observations. Future model development could improve upon the smooth fitting of the observed data.
Please explain time series bootstrapping. I don’t see how the uncertainty of the transient N2O concentration in a layer can be obtained by time series bootstrapping.
We will describe how time series bootstrapping was performed in our specific case in more detail in the revised manuscript. Briefly, time series bootstrapping was applied to calculate the standard error of the fitted values for N2O fluxes averaged at each time step for the smooth curve. Here, we considered general bootstrapping with a fixed block that generates replicate time series (e.g., 1000 times). Then the 95% confidence interval of estimated fluxes was computed, accordingly.
Equations (8) and (9): These equations are used to reflect both isotopic fractionation and mixing. However, the mixing part is necessarily mass / isotope conserving. I.e., it is only a valid approximation if Ftop, Fbot, N2Onit, N2Oden and N2Ored are small compared to N2Oconc,0. The reason is as follows: Assume that in (7), N2Onit 4 times N2Oconc,0 and SP0 is 0. The shift in SP would be 4 *34.4 per mil = 137.6 per mil. This is outright impossible. Consequently, the formulation as it is doesn’t ensure a physically sane mixing process as the highest possible shift would be limited to a shift that results in SP of 34.4 per mil for nitrification-derived N2O and 0 for denitrification. This means, the authors need to find criterions for the time step control or find a formulation that allows simultaneous fractionation and mixing calculations in a mathematically correct way.
Please see response in attachement. Our response includes equations that did not carry over well in the embedded response box.
L284: diffusion isotope effects have different sign and massively different magnitude. How can the isotope effect of diffusion be so different if the mass difference between 14N15N16O and 14N14N18O is only in the range of 1/46 ~ 2.1%? Considering the low inverse isotope effect of diffusion for SP and the inverse sign of d18O, I am wondering if these isotope effects are robust.
Thank you for this comment. We adopted isotope effects associated with diffusion from the literature. However, verifying the likelihood of the isotope effect of N2O diffusion is outside of the scope of this study. Future research could further investigate this matter.
L310-313: I fully agree that at small time steps, open and closed system calculations yield the same results. However, the adequate time step size depends on magnitudes of flux rates, N2O concentration and isotope effect. The authors have to at least show that results did not change significantly for different time steps or present a time step control.
We thank the reviewer for this suggestion. The change in N2O concentrations and isotope values over time is reflected in the derivative to the smooth curve at that time point. The system of equations was solved at each time point for which the derivative was calculated, which was chosen to be every day. However, as the smooth curve integrates between originally observed time points, the model outcome would not change if we changed the time step at which the system of equations is solved. There would just be less points in figures 3 and 4.
Results
L339: 0 to 30 ppm is a huge range. Were there amount effects, i.e., an effect of N2O mixing ratio on isotopic composition? Was this checked in any way? Please refer to it in your methods section.
Concentration dependencies during the measurement of the isotopic composition of N2O are overcome by tuning the IRMS to be linear across a range of concentrations. However, the IRMS in our lab is optimized for measuring a range between 0.3 to 3ppm. Therefore, concentrations higher than 3ppm were diluted down to be able to measure them accurately on the device.
L348: please change second “where” to “were”.
We will implement this change in the revised manuscript.
L352-354: it actually seems like a stark contrast to pulse emissions, but in the paper, I could not find soil-atmosphere N2O flux. Could you please provide the time series of the chamber flux measurements and integrate it in the publication?
We will include the time series of the N2O flux in supplementary materials.
L400: The uncertainty analysis is important, and very much appreciated. However, I am confused when looking at Figure 3. It seems like all variations in endmembers and input variables will result in lower production or consumption rates when rates are higher than 0.3 kg ha-1 day-1. Please explain this behavior. I assumed to see both positive and negative deviations. Is the used parameter set some unique constellation of values? At lower rates, the model doesn’t seem robust (see values after day 100) at which relative deviation of fitted rates are massive. This needs to be discussed.
We will expand on the sensitivity analysis in the revised manuscript and test the impact of uncertainty around endmembers in several depths and lysimeters, to provide a more comprehensive overview of whether this behavior is systematic or not. We will also redo all analysis to include the most current end-member values published in Yu et al. 2020. The discussion will be elaborated on accordingly.
Discussion
L460-462: whether or not soils are net sinks or sources for N2O is a fundamentally important question. The model results of net N2O uptake from the atmosphere contradict the observation of typical N2O emission rates. At this point, the authors need to further investigate possible reasons. One striking aspect is already shown in Figure 3: Nitrification- and denitrification-related N2O emissions were lower if uncertainty in endmembers or input variables (bulk density, soil moisture, N2O concentrations and isotopic composition) was considered. This may indicate that different endmembers or input parameters may decrease the discrepancy of gross production and consumption. The model should for sure be constrained in a way that the surface fluxes are reproduced by the model.
We agree with the reviewer that whether soils are a net source or sink of N2O is an important issue. We will explore the impacts of changing bulk density or end members in more detail in the revised manuscript and elaborate on it in the discussion. Meanwhile, we argue that N2O surface fluxes and gross N2 production operate at different orders of magnitude, and that different approaches may be needed to unravel these two research gaps in more detail. The focus of this study was to propose a method to estimate gross N2 loss from the soil profile, in the context of constraining ecosystem N budgets. If the focus is to estimate net N2O fluxes from the surface, flux chambers or eddy covariance methods are much more direct measurements and therefore more appropriate.
In addition, the figures lack indication of fertilizer application. Was fertilizer application associated with soil-atmosphere fluxes?
We will include surface fluxes and indications of fertilizer application in supporting information in the revised manuscript.
L497-499: Decoupling is one possibility, but alternatively, N2O production pulses in a top soil layer may be concealed due to the low sampling rate. This may be a consequence of the shorter travelling time of a N2O molecule that is produced close to the soil atmosphere boundary. Higher soil moisture at lower depths may decrease transport rates out of the soil.
We will add this suggestion to the revised manuscript.
Conclusion
L527-528: I don’t agree that your model has necessarily constrained total denitrification, especially since total soil-atmosphere exchange could not be reflected. Your study has definitely shown that N2O production needs to be largely balanced by consuming processes. But you could not show in how far the solutions are accurate with regard to magnitude of fluxes.
We will change the phrasing to reflect this comment in the conclusion of the revised manuscript.
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