the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 11 Jan 2023
Carbon dynamics after five decades of different crop residue management in temperate climate
Abstract. Increasing soil organic carbon (SOC) in agricultural soils is nowadays receiving growing attention also due to the COP21 initiative of “4 per 1000”. In this study, the effect of five decades of different residue management (residue removal, residue incorporation, and residue incorporation + poultry manure) was investigated on SOC stock and related to the 4 per 1000 and C saturation concepts. Preliminary results showed that higher 0–60 cm SOC stock was found after 54 years of the experiment when residues were incorporated into the soil compared to residue removal (75.0 vs 69.0 t ha−1) while poultry manure had a negligible effect. Comparing the 0–30 cm SOC stock with pre-existent data series, a general decreasing trend was observed from the start of the experiment in 1966 up to 1986, being greater in residual removal (−8.6 t ha−1) than residual incorporation (−4.8 t ha−1, irrespective of poultry manure addition). In 2020, the difference between the above-mentioned systems was 4.1 t ha−1 corresponding to a 2.2 ‰ which is lower than what was suggested by the 4 per 1000 initiative. This SOC stock attributed to residue retention arose in response to 141 t C ha−1 residue resulting in a 0.1 % yearly conversion rate that is sensibly lower than what is generally reported in the literature. Therefore, an alternative use (e.g., bioenergy production) of at least part of crop residues is conceivable in temperate climate for a more efficient C cycle. The studied soil was demonstrated also to be far from C saturation, being in the 30−47 % degree of saturation range. Therefore, specific studies on how both organic and inorganic (i.e., carbonates) C fractions related to different soil aggregates and aggregate mineralization are namely requested.
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RC1: 'Comment on egusphere-2022-1497', Anonymous Referee #1, 15 Apr 2023
This paper reports soil organic carbon (SOC) concentrations and stocks from a long-term residue, manure, and fertilization experiment. The authors discuss the changes in SOC between residue and manure treatments and over time in the context of soil carbon saturation and the ‘4 per mille’ recommendation, providing the hypothesis that crop residue incorporation and poultry manure addition may be effective for fulfilling goals of ‘4 per mille’. While most of the data are novel and the general concept of reporting SOC levels in a long-term field experiment is sound, I have multiple concerns surrounding almost all aspects the of the sample collection, discussion of experimental design, data reporting, analytical methods, interpretations of results, and writing style.
Specific comments:
- Lack of clarity about number of cores taken per experimental plot for SOC analysis. The methods section is written in a way that it is not entirely clear how many soil cores were taken per plot, but it seems possible that there were 60 ‘disturbed’ cores taken in total, one for each experimental plot? If so, this is a strong limitation of the study. SOC is highly spatially heterogenous, so if one core per plot was sampled, even with 4 plot-level replicates of each treatment, this coring strategy would introduce likelihood that true differences in SOC levels due to treatment were not clearly observed and that reported differences reflect a large element of spatial heterogeneity across the field trial rather than showing treatment effects. If one core per plot was taken, while the sampling strategy cannot be altered at this stage, I would strongly suggest to the authors to clearly report the number of cores taken per plot for SOC analysis (e.g., “We sampled one core per plot for SOC analysis, and divided it into two depths”) rather than only total number of cores, and to justify this approach, and to acknowledge in the discussion section the limitations introduced into the detection of treatment differences by this likely under-sampling of the field trial.
- Confounding of tillage with residue retention in experimental design. The experimental design consisted of two treatments of residue incorporation (one with manure) and another with residue removal, at all levels of N fertilization, where only the treatment of residue removal was not disturbed, thus presenting a confounding effect of tillage with residue. Tillage can affect amount and distribution of SOC. While this long-term treatment is not under the control of the authors, the rationale for the experimental design, its drawbacks, and the ambiguity it introduces into interpretation of the results should nevertheless be carefully discussed.
- Use of different analytical methods to measure SOC over time. The authors report pre-existing data from a time series of SOC sampling at the site, where earlier samples were assessed with the dichromate oxidation method and later samples were analyzed with a flash combustion method. Different analysis methods for SOC return different results for the same soils (Roper et al. 2019 https://doi.org/10.2136/sssaj2018.03.0105); while the authors performed a methods comparison with this in mind, the results of this comparison are not reported (paragraph line 115). I suggest that the authors report summary statistics and show data, possibly in supplementary materials, of their methods comparison tests and also incorporate a discussion of how the interpretation of time series data may be affected by variability and especially bias introduced by the different SOC analysis methods.
- Non-reporting of effect of N fertilization on SOC stocks. While the authors only report SOC levels per residue and manure addition treatment, there were five levels of N fertilization also sampled. In Figures 1-3, which N fertilization levels are represented? Or, are N fertilization levels averages across residue and manure treatments? Please specify in the methods and in the figure legends.
- Non-reporting of C input estimates. Although a calculation of C inputs is discussed in the methods section and reported in the abstract, the data on C inputs across treatments are not currently reported in any table, or figure, or in the results section. Please add these results.
- Absence of results section corresponding to Figure 3 (SOC change over time). The authors present Figure 3 in the discussion section, and these data are discussed in the abstract and conclusions, but currently there is not a results section corresponding to this figure. I suggest the authors either expand existing results sections to include results reporting for this figure, or create a new results section.
- Overall lack of legibility of data visualization. Particularly in Figure 2, the shadings used for different depths can’t be discerned from the legend. The caption in Figure 2 doesn’t specify if post-hoc comparisons represented by letters are across treatments within the same depth; this seems likely but could be clarified (same in Figure 1). In Figure 1, larger font size for axis labels would improve readability.
- Claim of testing the soil carbon saturation concept: the authors use previous literature to calculate the expected maximum of soil organic carbon in mineral-associated form (MAOC) based on soil texture at the experimental site, and reasonably point out that the SOC levels observed were below the expected theoretical maximum, and therefore far from saturation. While their conclusion is probably sound, there are several conceptual and analytical flaws with the work, and a more nuanced approach and discussion would improve the rigor of the interpretation and claims. First, the concept of soil carbon saturation applies specifically to the mineral-associated carbon (MAOC), isolated through soil disturbance and size or density cutoffs. However, the authors measure and report only total soil organic carbon, which also includes particulate organic carbon (POC) that is not theorized to be controlled by saturation limits. Since the SOC (=MAOC + POC) reported is still below the theoretical maximum of MAOC based on soil texture, the claim that the soils were below saturation (based on this theory and method accounting) is still accurate, but it needs to be acknowledged the implications of the presence of POC in the sample and how this affects the saturation estimate. Second, the authors use older references for their calculation of MAOC at saturation; why use these rather than larger and more recent datasets? E.g., Feng et al. 2013 1007/s10533-011-9679-7; Georgiou et al. 2022 10.1038/s41467-022-31540-9.
- Interpretation of 4 per mille objective based on last SOC sampling only, when all treatments studied appear to decrease in SOC over time. The efficacy of 4 per mille and other natural climate solutions depends on increasing SOC levels, so the results of the time series, so long as they are based on sound inter-method comparison, would represent a repudiation of the 4 per mille at this site.
- Thoroughness and logic of various data interpretations. The authors find no effect of adding poultry manure on SOC, which is surprising given that exogenous C sources have previously been found to be highly effective in increasing local SOC levels. However, the rate of poultry manure dry matter addition is much lower than normally studied (1 Mg / ha annually; in meta-analysis of Kallenbach et al 2011 doi:10.1016/j.agee.2011.08.020, 5 Mg / ha is lowest dry matter addition category), which is not currently contextualized. Near L200, the authors claim that the experimental site was not a SOC equilibrium, “confirmed by the low C/N ratios”; how can C/N ratios be used to infer a non-equilibrium state? Near L250, the authors claim how, in general, calcaric, silty soils are inert to management practices because they are compacted and sometimes anoxic, but how are any of these characteristics grounds for a soil being unresponsive to management practices? Near L255, the authors claim that SOC levels declined in the study as a result of ‘agricultural intensification’, but different levels of agricultural intensification were not clearly compared in the study, so how could this statement factor so prominently in their conclusions?
- Writing style. The manuscript writing, in terms of structure and style does not yet meet a high standard of quality. Paragraph structure is not consistently used, as some sentences are presented outside of paragraphs (last sentence of introduction; second sentence of section 2.2; last sentence of section 3.1). The meaning of ‘sensibly’ as a modifier, repeatedly used, is unclear. Parts of the manuscript are written in an informal or casual style that should be revised in order to be suitable for publication in a scientific journal (“Anyway”, “Nowadays”).
Citation: https://doi.org/10.5194/egusphere-2022-1497-RC1 - AC1: 'Reply on RC1', Ilaria Piccoli, 20 Jun 2023
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RC2: 'Comment on egusphere-2022-1497', Anonymous Referee #2, 17 Apr 2023
General Comments –
The manuscript submitted by Piccoli et al. presents the results of a 54 year long field experiment, with a focus on soil carbon accumulation in response to residue management treatments. Using mixed models, the authors attempt to understand how residue incorporation drives soil C and N stocks and concentrations, and then apply a series of empirical models for determining soil C saturation to explain their findings. Additionally, they examine the time-series of data stretching back to 1966 to understand the long-term impacts of the residue management treatments. The authors find that residue removal did significantly decrease SOC stocks relative to residue incorporation treatments, though the general trend of the SOC stocks since the experiments inception has been a loss. They find little evidence of saturation across the models they employ. Overall, the authors present an interesting and important dataset that should continue to be investigated, as long-term SOC datasets continue to be sparse. There are several issues that bar the manuscript from publication in its current form, however. The writing style is often overly casual, and does not adhere to typical paragraph form, making the reading of the MS somewhat confusing and choppy. In addition, the methods are not plainly described, leading to a difficulty on the part of the reader to evaluate the authors results. This is most relevant in the discussion of sampling, the calculations of the saturation values, and the rationale for the statistical tests that were employed. The results section is relatively brief, while some data, such as the time-series results, are not introduced at all until the discussion. Other data that are relevant the the conclusions drawn, such as the impact of N rate or the interaction effect between N rate and residue treatment, are not presented at all. The concluding statements of the manuscript introduce new concepts as well, not previously discussed throughout the paper. Finally, the MS is either incomplete or contains errors, as Table 1 is not included in the text, despite in-text references. I’ve detailed my specific comments below.
Specific Line Edits-
Lines 28 – 30: Do you think this assertion holds up across all ecosystems? I agree that the mineral-associated fraction has a finite upper limit on its accumulation, but see Cotrufo et al. 2019 for evidence of particulate organic matter accumulation that lacks a saturation limit.
Lines 39-43: There’s been a lot of recent work on saturation behavior in soil carbon (e.g., Georgiou et al., 2022; Heckman et al., 2023) that is relevant to the present study. I recommend the authors broaden the scope of their literature review in this section to include both the foundational and contemporary literature.
Line 53: There was a rapid shift in subject here that was hard to follow as a reader. I recommend the authors consider restructuring this paragraph to better communicate the ideas presented.
Lines 89-91: Please describe the overall tillage management for each plot here. It is currently unclear how tillage is handled between treatments – does the residue removal treatment receive the same level of cultivation as the incorporation and manure treatments? If not, please describe how this has been accounted for in the resulting analysis.
Lines 99 – 103: I found the description of sampling here to be confusing. Two things in particular stand out: First, did the authors collect one sample per plot? Right now, that is not clear from the text, which implies that 60 samples were taken per plot. Second, were two sets of samples taken, one for bulk density and one for elemental analysis? Or was the original sample used for both analyses?
Line 111: I believe that the experimental design the authors have described is a randomized complete block, split-plot design, which residue management the main plot effect, and N rate treatment as the split-plot effect. Did the authors consider this when designing the error structure of their mixed model? More directly, shouldn’t there be an additional random effect that specifies the nested structure of the design and specifies random intercepts for the block/residue/N rate combination?
Line 120: As mentioned above, several recent papers have provided updated means for understanding soil C saturation and saturation deficit (Georgieo et al., 2022 in particular). Please provide some rationale for the use of the Hassink and Dexter models in lieu of the more contemporaneous approaches, either in response or in the text.
Lines 123 – 125: Please show the equations for the saturation models that you employ here such that they can be referenced during the reading of the results.
Line 136: Is there an established agronomic optimum N rate for this site? If so, does it inform at all the relationship between SOC and N rate?
Lines 170 – 175: Is there a description of how the authors either isolated or estimated the different soil particle size class distributions used in these models? Please describe this process and include in the methods section.
Line 184: None of the time-series data is presented in the Results section, which makes its introduction here somewhat surprising and confusing. I encourage the authors to add these data and the results that they glean from it to the results section prior to discussing it here.
Line 195: I’m confused as to why the x-axis on this plot extends to 2030. If the authors aren’t projecting out to that date, I suggest that reformat the axis to represent the data that they have available and are presenting.
Lines 198 – 199: Please provide further explanation as to your assertion here, that a lower CN ratio in 1966 is evidence that the system was out of equilibrium.
Lines 209 – 211: I’m a little confused here – are the authors suggesting there is a biophysical limitation on the ability to maintain carbon stores over time? Unless I’m misinterpreting, does this imply that agricultural systems are restricted from reaching a steady state, even over the course of decades?
Lines 224 – 228: This is an interesting point, but I’m not sure how it’s relevant to the question at hand regarding the potential of reaching the 4 per mille goal via residue incorporation. I recommend the authors make the linkage more explicit here. Further, I’m not sure this accounting is fully inclusive. Given the results from above, that over the course of the experiment residue removal has lost significantly more carbon that residue incorporated treatments, would you still arrive at this results if you factored in the lost soil C in addition? I could be misunderstanding the math the authors use here, but I would appreciate their clarification.
Lines 232-233: Please clarify this statement, as in lines 135 and 154 the authors state that N rate does affect both C concentrations and stocks.
Line 244: Where is Table 1? The authors have not included it in the present manuscript, limiting the interpretation of the results they discuss here.
Line 264 – 267: The authors here are presenting the discussion of carbonates as though this is a central finding from the manuscript, but this is the first time that it is discussed. Additional text is needed in the discussion section for the reader to have the context necessary to interpret this.
Citation: https://doi.org/10.5194/egusphere-2022-1497-RC2 - AC2: 'Reply on RC2', Ilaria Piccoli, 20 Jun 2023
Status: closed
-
RC1: 'Comment on egusphere-2022-1497', Anonymous Referee #1, 15 Apr 2023
This paper reports soil organic carbon (SOC) concentrations and stocks from a long-term residue, manure, and fertilization experiment. The authors discuss the changes in SOC between residue and manure treatments and over time in the context of soil carbon saturation and the ‘4 per mille’ recommendation, providing the hypothesis that crop residue incorporation and poultry manure addition may be effective for fulfilling goals of ‘4 per mille’. While most of the data are novel and the general concept of reporting SOC levels in a long-term field experiment is sound, I have multiple concerns surrounding almost all aspects the of the sample collection, discussion of experimental design, data reporting, analytical methods, interpretations of results, and writing style.
Specific comments:
- Lack of clarity about number of cores taken per experimental plot for SOC analysis. The methods section is written in a way that it is not entirely clear how many soil cores were taken per plot, but it seems possible that there were 60 ‘disturbed’ cores taken in total, one for each experimental plot? If so, this is a strong limitation of the study. SOC is highly spatially heterogenous, so if one core per plot was sampled, even with 4 plot-level replicates of each treatment, this coring strategy would introduce likelihood that true differences in SOC levels due to treatment were not clearly observed and that reported differences reflect a large element of spatial heterogeneity across the field trial rather than showing treatment effects. If one core per plot was taken, while the sampling strategy cannot be altered at this stage, I would strongly suggest to the authors to clearly report the number of cores taken per plot for SOC analysis (e.g., “We sampled one core per plot for SOC analysis, and divided it into two depths”) rather than only total number of cores, and to justify this approach, and to acknowledge in the discussion section the limitations introduced into the detection of treatment differences by this likely under-sampling of the field trial.
- Confounding of tillage with residue retention in experimental design. The experimental design consisted of two treatments of residue incorporation (one with manure) and another with residue removal, at all levels of N fertilization, where only the treatment of residue removal was not disturbed, thus presenting a confounding effect of tillage with residue. Tillage can affect amount and distribution of SOC. While this long-term treatment is not under the control of the authors, the rationale for the experimental design, its drawbacks, and the ambiguity it introduces into interpretation of the results should nevertheless be carefully discussed.
- Use of different analytical methods to measure SOC over time. The authors report pre-existing data from a time series of SOC sampling at the site, where earlier samples were assessed with the dichromate oxidation method and later samples were analyzed with a flash combustion method. Different analysis methods for SOC return different results for the same soils (Roper et al. 2019 https://doi.org/10.2136/sssaj2018.03.0105); while the authors performed a methods comparison with this in mind, the results of this comparison are not reported (paragraph line 115). I suggest that the authors report summary statistics and show data, possibly in supplementary materials, of their methods comparison tests and also incorporate a discussion of how the interpretation of time series data may be affected by variability and especially bias introduced by the different SOC analysis methods.
- Non-reporting of effect of N fertilization on SOC stocks. While the authors only report SOC levels per residue and manure addition treatment, there were five levels of N fertilization also sampled. In Figures 1-3, which N fertilization levels are represented? Or, are N fertilization levels averages across residue and manure treatments? Please specify in the methods and in the figure legends.
- Non-reporting of C input estimates. Although a calculation of C inputs is discussed in the methods section and reported in the abstract, the data on C inputs across treatments are not currently reported in any table, or figure, or in the results section. Please add these results.
- Absence of results section corresponding to Figure 3 (SOC change over time). The authors present Figure 3 in the discussion section, and these data are discussed in the abstract and conclusions, but currently there is not a results section corresponding to this figure. I suggest the authors either expand existing results sections to include results reporting for this figure, or create a new results section.
- Overall lack of legibility of data visualization. Particularly in Figure 2, the shadings used for different depths can’t be discerned from the legend. The caption in Figure 2 doesn’t specify if post-hoc comparisons represented by letters are across treatments within the same depth; this seems likely but could be clarified (same in Figure 1). In Figure 1, larger font size for axis labels would improve readability.
- Claim of testing the soil carbon saturation concept: the authors use previous literature to calculate the expected maximum of soil organic carbon in mineral-associated form (MAOC) based on soil texture at the experimental site, and reasonably point out that the SOC levels observed were below the expected theoretical maximum, and therefore far from saturation. While their conclusion is probably sound, there are several conceptual and analytical flaws with the work, and a more nuanced approach and discussion would improve the rigor of the interpretation and claims. First, the concept of soil carbon saturation applies specifically to the mineral-associated carbon (MAOC), isolated through soil disturbance and size or density cutoffs. However, the authors measure and report only total soil organic carbon, which also includes particulate organic carbon (POC) that is not theorized to be controlled by saturation limits. Since the SOC (=MAOC + POC) reported is still below the theoretical maximum of MAOC based on soil texture, the claim that the soils were below saturation (based on this theory and method accounting) is still accurate, but it needs to be acknowledged the implications of the presence of POC in the sample and how this affects the saturation estimate. Second, the authors use older references for their calculation of MAOC at saturation; why use these rather than larger and more recent datasets? E.g., Feng et al. 2013 1007/s10533-011-9679-7; Georgiou et al. 2022 10.1038/s41467-022-31540-9.
- Interpretation of 4 per mille objective based on last SOC sampling only, when all treatments studied appear to decrease in SOC over time. The efficacy of 4 per mille and other natural climate solutions depends on increasing SOC levels, so the results of the time series, so long as they are based on sound inter-method comparison, would represent a repudiation of the 4 per mille at this site.
- Thoroughness and logic of various data interpretations. The authors find no effect of adding poultry manure on SOC, which is surprising given that exogenous C sources have previously been found to be highly effective in increasing local SOC levels. However, the rate of poultry manure dry matter addition is much lower than normally studied (1 Mg / ha annually; in meta-analysis of Kallenbach et al 2011 doi:10.1016/j.agee.2011.08.020, 5 Mg / ha is lowest dry matter addition category), which is not currently contextualized. Near L200, the authors claim that the experimental site was not a SOC equilibrium, “confirmed by the low C/N ratios”; how can C/N ratios be used to infer a non-equilibrium state? Near L250, the authors claim how, in general, calcaric, silty soils are inert to management practices because they are compacted and sometimes anoxic, but how are any of these characteristics grounds for a soil being unresponsive to management practices? Near L255, the authors claim that SOC levels declined in the study as a result of ‘agricultural intensification’, but different levels of agricultural intensification were not clearly compared in the study, so how could this statement factor so prominently in their conclusions?
- Writing style. The manuscript writing, in terms of structure and style does not yet meet a high standard of quality. Paragraph structure is not consistently used, as some sentences are presented outside of paragraphs (last sentence of introduction; second sentence of section 2.2; last sentence of section 3.1). The meaning of ‘sensibly’ as a modifier, repeatedly used, is unclear. Parts of the manuscript are written in an informal or casual style that should be revised in order to be suitable for publication in a scientific journal (“Anyway”, “Nowadays”).
Citation: https://doi.org/10.5194/egusphere-2022-1497-RC1 - AC1: 'Reply on RC1', Ilaria Piccoli, 20 Jun 2023
-
RC2: 'Comment on egusphere-2022-1497', Anonymous Referee #2, 17 Apr 2023
General Comments –
The manuscript submitted by Piccoli et al. presents the results of a 54 year long field experiment, with a focus on soil carbon accumulation in response to residue management treatments. Using mixed models, the authors attempt to understand how residue incorporation drives soil C and N stocks and concentrations, and then apply a series of empirical models for determining soil C saturation to explain their findings. Additionally, they examine the time-series of data stretching back to 1966 to understand the long-term impacts of the residue management treatments. The authors find that residue removal did significantly decrease SOC stocks relative to residue incorporation treatments, though the general trend of the SOC stocks since the experiments inception has been a loss. They find little evidence of saturation across the models they employ. Overall, the authors present an interesting and important dataset that should continue to be investigated, as long-term SOC datasets continue to be sparse. There are several issues that bar the manuscript from publication in its current form, however. The writing style is often overly casual, and does not adhere to typical paragraph form, making the reading of the MS somewhat confusing and choppy. In addition, the methods are not plainly described, leading to a difficulty on the part of the reader to evaluate the authors results. This is most relevant in the discussion of sampling, the calculations of the saturation values, and the rationale for the statistical tests that were employed. The results section is relatively brief, while some data, such as the time-series results, are not introduced at all until the discussion. Other data that are relevant the the conclusions drawn, such as the impact of N rate or the interaction effect between N rate and residue treatment, are not presented at all. The concluding statements of the manuscript introduce new concepts as well, not previously discussed throughout the paper. Finally, the MS is either incomplete or contains errors, as Table 1 is not included in the text, despite in-text references. I’ve detailed my specific comments below.
Specific Line Edits-
Lines 28 – 30: Do you think this assertion holds up across all ecosystems? I agree that the mineral-associated fraction has a finite upper limit on its accumulation, but see Cotrufo et al. 2019 for evidence of particulate organic matter accumulation that lacks a saturation limit.
Lines 39-43: There’s been a lot of recent work on saturation behavior in soil carbon (e.g., Georgiou et al., 2022; Heckman et al., 2023) that is relevant to the present study. I recommend the authors broaden the scope of their literature review in this section to include both the foundational and contemporary literature.
Line 53: There was a rapid shift in subject here that was hard to follow as a reader. I recommend the authors consider restructuring this paragraph to better communicate the ideas presented.
Lines 89-91: Please describe the overall tillage management for each plot here. It is currently unclear how tillage is handled between treatments – does the residue removal treatment receive the same level of cultivation as the incorporation and manure treatments? If not, please describe how this has been accounted for in the resulting analysis.
Lines 99 – 103: I found the description of sampling here to be confusing. Two things in particular stand out: First, did the authors collect one sample per plot? Right now, that is not clear from the text, which implies that 60 samples were taken per plot. Second, were two sets of samples taken, one for bulk density and one for elemental analysis? Or was the original sample used for both analyses?
Line 111: I believe that the experimental design the authors have described is a randomized complete block, split-plot design, which residue management the main plot effect, and N rate treatment as the split-plot effect. Did the authors consider this when designing the error structure of their mixed model? More directly, shouldn’t there be an additional random effect that specifies the nested structure of the design and specifies random intercepts for the block/residue/N rate combination?
Line 120: As mentioned above, several recent papers have provided updated means for understanding soil C saturation and saturation deficit (Georgieo et al., 2022 in particular). Please provide some rationale for the use of the Hassink and Dexter models in lieu of the more contemporaneous approaches, either in response or in the text.
Lines 123 – 125: Please show the equations for the saturation models that you employ here such that they can be referenced during the reading of the results.
Line 136: Is there an established agronomic optimum N rate for this site? If so, does it inform at all the relationship between SOC and N rate?
Lines 170 – 175: Is there a description of how the authors either isolated or estimated the different soil particle size class distributions used in these models? Please describe this process and include in the methods section.
Line 184: None of the time-series data is presented in the Results section, which makes its introduction here somewhat surprising and confusing. I encourage the authors to add these data and the results that they glean from it to the results section prior to discussing it here.
Line 195: I’m confused as to why the x-axis on this plot extends to 2030. If the authors aren’t projecting out to that date, I suggest that reformat the axis to represent the data that they have available and are presenting.
Lines 198 – 199: Please provide further explanation as to your assertion here, that a lower CN ratio in 1966 is evidence that the system was out of equilibrium.
Lines 209 – 211: I’m a little confused here – are the authors suggesting there is a biophysical limitation on the ability to maintain carbon stores over time? Unless I’m misinterpreting, does this imply that agricultural systems are restricted from reaching a steady state, even over the course of decades?
Lines 224 – 228: This is an interesting point, but I’m not sure how it’s relevant to the question at hand regarding the potential of reaching the 4 per mille goal via residue incorporation. I recommend the authors make the linkage more explicit here. Further, I’m not sure this accounting is fully inclusive. Given the results from above, that over the course of the experiment residue removal has lost significantly more carbon that residue incorporated treatments, would you still arrive at this results if you factored in the lost soil C in addition? I could be misunderstanding the math the authors use here, but I would appreciate their clarification.
Lines 232-233: Please clarify this statement, as in lines 135 and 154 the authors state that N rate does affect both C concentrations and stocks.
Line 244: Where is Table 1? The authors have not included it in the present manuscript, limiting the interpretation of the results they discuss here.
Line 264 – 267: The authors here are presenting the discussion of carbonates as though this is a central finding from the manuscript, but this is the first time that it is discussed. Additional text is needed in the discussion section for the reader to have the context necessary to interpret this.
Citation: https://doi.org/10.5194/egusphere-2022-1497-RC2 - AC2: 'Reply on RC2', Ilaria Piccoli, 20 Jun 2023
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