the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 03 Mar 2021
High greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon
Abstract. Amazonian peat swamp forests remove large amounts of carbon dioxide (CO2) but anaerobic decomposition of the peat produces methane (CH4). Drought or cultivation cuts down on the CH4 production but may increase the CO2 emission. Varying oxygen content in nitrogen-rich peat produces nitrous oxide (N2O). Despite the potentially tremendous changes, greenhouse gas emissions from peatlands under various land uses and environmental conditions have rarely been compared in the Amazon. We measured CO2, CH4 and N2O emissions from the soil surface with manual opaque chambers, and environmental characteristics in three sites around Iquitos, Peru from September 2019 to March 2020: a pristine peat swamp forest, a young forest and a slash-and-burn manioc field. The manioc field showed moderate peat respiration and N2O emission. The swamp forests under slight water table drawdown emitted large amounts of CO2 and N2O while retaining their high CH4 emissions. Most noticeably, a heavy shower after the water-table drawdown in the pristine swamp forest created a hot moment of N2O. Nitrifier denitrification was the likely source mechanism, as we rule out nitrification and heterotrophic denitrification. We base the judgement on the lack of nitrate and oxygen, and the suppressed denitrification potential in the topsoil. Overall, our study shows that even moderate drying in Peruvian palm swamps may create a devastating feedback on climate change through CO2 and N2O emissions.
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RC1: 'Comment on bg-2021-46', Yit Arn Teh, 25 Mar 2021
GENERAL COMMENTS
This is a topically relevant paper, given how little is known about peatlands in South America, and growing interest in understanding how tropical peatland management worldwide influences regional and global exchanges of greenhouse gases. This paper adds to the growing body of knowledge on the biogeochemistry of South America peatlands, and nicely integrates field-based flux measurements with more process-based laboratory assays. However, while I am broadly supportive of this paper, I think that the paper needs to be revised in order to enhance reader understanding and to acknowledge potential limitations with the experimental methods and design.
First and foremost, given that this study is of limited geographic scope, with data collected over a relatively narrow window of time (i.e. only 6 months of measurements), the authors need to do more to acknowledge that it may be difficult to generalise their findings to larger spatial domains or longer periods of time. For example, I was concerned that the authors were over-reaching when they extrapolated their data over the entire Pastaza-Marañon foreland basin region (see point 10 below).
Second, the authors need to clarify for non-expert readers if their measurements captured both wet and dry seasons (see point 4 below), given that water table depth and other environmental conditions vary substantially between wet and dry seasons, with a strong wet/dry season signal in CH4 and other trace gas emissions detectable not only from Amazon-basin wide studies of atmospheric chemistry and from smaller scale, site level studies of ecosystem gas exchange (e.g. Wilson et al. 2016). Seasonal affects will have ramifications not only for their field data, but could also influence their incubation results, as water table and other environmental conditions will influence the status of the microbial community at the time of soil collection; e.g. soils collected for incubation during the wet season could have a different activity profile or functional composition from the same soils collected during the dry season.
Third, the cold storage of soil for incubations is problematic and could lead to significant treatment effects (point 8). Historic studies by Louis Verchot, Marife Corre, Ed Veldkamp and others have demonstrated adverse impacts on N cycling microbes (relevant to this study given it’s focus on N2O), and many tropical research teams now transport soils at room temperature or conduct laboratory experiments near their field sites to avoid these treatment effects. While potential treatment effects do not invalidate the incubation studies presented here, the authors need to acknowledge the potential issues caused by cold storage and discuss how this may impact their interpretation of the results.
Fourth, on a more technical point, the authors need to clarify how they treated non-linear data and chambers that show potential evidence of ebullition. Fitting linear curves to non-linear data or excluding ebullition data will tend to underestimate flux rates.
Specific comments are provided in the section below.
SPECIFIC COMMENTS
- Lines 70-72: Since this study only investigated a sub-set of land-uses in the region, it would be clearer and more transparent if the authors indicated here which land-use types they focused on in this paper, with a brief justification for why they have concentrated on these land-uses in particular.
- Lines 76-80: For readers unfamiliar with the Roucoux et al. (2013) paper, I recommend expanding the site description for the human-affected sites so it’s clearer how human intervention has altered these study sites.
- Lines 91-93: Please clarify how many samples were collected over a 60 minute period; i.e. 4 time points (0, 20, 40, 60 minutes) or 3 (20, 40, 60 minutes).
- Lines 95-96: Did these sampling campaigns cover both wet and dry seasons? This is not clear - please clarify this in the narrative. Also indicate in Table 1 what season the campaigns were conducted in so it’s clearer if there was even sampling between seasons.
- Lines 101-102: How was CO2 determined? Did the instrument have a methanizer? Also – N2 flux is mentioned in the Results and Discussion section, but it’s not clear how N2 was measured in the field flux measurements – this must be clarified.
- Lines 102-104: How were non-linear data treated or chambers which showed evidence of ebullition (i.e. erratic or very large non-linear changes in concentration)? Were these data discarded or included?
- Line 106: Treating non-detectable fluxes as zeroes (rather than as a “n/a” or flux at the limit of detection) is a judgement call, given that there is a line of reasoning which argues that treating these data as zeroes biases your dataset towards zero values, when in fact these data points may be producing/consuming gases below the limit of detection. I recommend that the authors provide some justification for this judgement call, given that this is a non-trivial decision.
- Line 116 and line 128: It is important to recognise that storage of tropical soils at low temperatures can negatively influence soil microbial communities and microbial activity, given that tropical microorganisms are not cold-adapted and can be severely impacted by storage at sub-ambient temperatures. There is quite a long history of research on this topic, and I recommend that the authors familiarise themselves with the peer-reviewed literature on this topic. The search string “cold storage tropical soil microbial activity” in Google Scholar produces at least half a dozen relevant references, including historic papers by Verchot (1999) Soil Sci Soc Am J and Arnold et al. (2008) Soil Bio Biochem on the effects of cold storage on N cycling in in tropical soils.
- Line 201: Mention of DNDC at this point in the narrative comes from left-field, since DNDC and modelling were not discussed before this. It’s not clear from the narrative if the authors used DNDC in their research or if they are drawing on findings from modelling studies to interpret their findings. This needs to be clarified as it is confusing.
- Lines 251-255: Given the small geographical and temporal scope of this study, I think that the authors are over-reaching when they upscale their fluxes to the entire basin. While these kinds of back of the envelope exercises are interesting and important for progressing the discussion, I think the authors need to be more circumspect about the claims they are making. In this instance, I recommend that the authors revise these sentence construction to make it clear that these numbers are highly speculative and represent first order estimates to gauge relative importance. To be clear, I’m not necessarily saying that the authors should remove these calculations, but rather they should change the language so it’s clear that there estimates are a speculative exercise, rather than certain predictions of the emissions potential of the basin.
- Lines 147-261: With respect to reporting fluxes in the body of the text, and I recommend that the authors make it clear when they are referring to field data or incubation data, given that results from laboratory incubations are often not directly comparable to field measurements because of differences in measurement scale, methodology, different handling/treatment effects, and problems of comparing open system (field) versus closed system (laboratory) measurements. The paper as it is currently written doesn’t clearly distinguish between data from these two different types of studies.
Citation: https://doi.org/10.5194/bg-2021-46-RC1 -
AC1: 'Reply on RC1', Jaan Pärn, 11 Jul 2021
RC1
GENERAL COMMENTS
This is a topically relevant paper, given how little is known about peatlands in South America, and growing interest in understanding how tropical peatland management worldwide influences regional and global exchanges of greenhouse gases. This paper adds to the growing body of knowledge on the biogeochemistry of South America peatlands, and nicely integrates field-based flux measurements with more process-based laboratory assays. However, while I am broadly supportive of this paper, I think that the paper needs to be revised in order to enhance reader understanding and to acknowledge potential limitations with the experimental methods and design.
Thank you for the supportive comment! We will revise the manuscript accordingly.
First and foremost, given that this study is of limited geographic scope, with data collected over a relatively narrow window of time (i.e. only 6 months of measurements), the authors need to do more to acknowledge that it may be difficult to generalise their findings to larger spatial domains or longer periods of time. For example, I was concerned that the authors were over-reaching when they extrapolated their data over the entire Pastaza-Marañon foreland basin region (see point 10 below).
Agreed. We originally intended the upscaling intended as a general guideline to the reader for context of our numbers, not a central point of the paper. We will remove the upscaling.
Second, the authors need to clarify for non-expert readers if their measurements captured both wet and dry seasons (see point 4 below), given that water table depth and other environmental conditions vary substantially between wet and dry seasons, with a strong wet/dry season signal in CH4 and other trace gas emissions detectable not only from Amazon-basin wide studies of atmospheric chemistry and from smaller scale, site level studies of ecosystem gas exchange (e.g. Wilson et al. 2016). Seasonal affects will have ramifications not only for their field data, but could also influence their incubation results, as water table and other environmental conditions will influence the status of the microbial community at the time of soil collection; e.g. soils collected for incubation during the wet season could have a different activity profile or functional composition from the same soils collected during the dry season.
We are wary to attribute any seasons to our measurement time. The start of our study period in September 2019 is most accurately described as the end of the dry season. However, the ensuing rains only lasted up until late December. The area received hardly any rain from January till March. The water table, however, remained high and stable during the January till March observations, due to the buffering effect of the peat and adjacent Lake Quistococha. We assume the microbial community responded to the immediate environmental conditions, not the multi-annual average pattern of seasons.
Third, the cold storage of soil for incubations is problematic and could lead to significant treatment effects (point 8). Historic studies by Louis Verchot, Marife Corre, Ed Veldkamp and others have demonstrated adverse impacts on N cycling microbes (relevant to this study given it’s focus on N2O), and many tropical research teams now transport soils at room temperature or conduct laboratory experiments near their field sites to avoid these treatment effects. While potential treatment effects do not invalidate the incubation studies presented here, the authors need to acknowledge the potential issues caused by cold storage and discuss how this may impact their interpretation of the results.
We will provide information on the transport, storage, and acclimatisation of the intact soil cores in the Material and Methods section. The bottom line is that the incubations showed various denitrification rates unrelated to sampling time but related to their ambient environmental conditions.
Fourth, on a more technical point, the authors need to clarify how they treated non-linear data and chambers that show potential evidence of ebullition. Fitting linear curves to non-linear data or excluding ebullition data will tend to underestimate flux rates.
We closely examined all our gas concentration trends in each individual chambers. Practically all significant deviations from a linear trend were apparently caused by a faulty chamber sealing. We did not observe any signs of ebullition such as jump rises in concentration not followed by a drop in concentration. An unnoticeable share of ebullition may be a peculiarity of our long chamber closing time of 1 hour.
Specific comments are provided in the section below.
SPECIFIC COMMENTS
Lines 70-72: Since this study only investigated a sub-set of land-uses in the region, it would be clearer and more transparent if the authors indicated here which land-use types they focused on in this paper, with a brief justification for why they have concentrated on these land-uses in particular.
We will clarify the targeted land uses better, both here and the Material and Methods section.
Lines 76-80: For readers unfamiliar with the Roucoux et al. (2013) paper, I recommend expanding the site description for the human-affected sites so it’s clearer how human intervention has altered these study sites.
We will expand the site description accordingly.
Lines 91-93: Please clarify how many samples were collected over a 60 minute period; i.e. 4 time points (0, 20, 40, 60 minutes) or 3 (20, 40, 60 minutes).
We will specify that we took a 0-sample at the start of every 1 h session.
Lines 95-96: Did these sampling campaigns cover both wet and dry seasons? This is not clear - please clarify this in the narrative. Also indicate in Table 1 what season the campaigns were conducted in so it’s clearer if there was even sampling between seasons.
See the comment on seasonality in the General Comments.
Lines 101-102: How was CO2 determined? Did the instrument have a methanizer?
The GC-2014 does not have a methaniser. We will specify that CO2 was also determined with the flame ionisation detector.
Also – N2 flux is mentioned in the Results and Discussion section, but it’s not clear how N2 was measured in the field flux measurements – this must be clarified.
The protocol for N2 denitrification potential determination is specified in lines 128–139.
Lines 102-104: How were non-linear data treated or chambers which showed evidence of ebullition (i.e. erratic or very large non-linear changes in concentration)? Were these data discarded or included?
We closely examined all our gas concentration trends in each individual chambers. Practically all significant deviations from a linear trend were apparently caused by a faulty chamber sealing. We did not observe any signs of ebullition such as jump rises in concentration not followed by a drop in concentration. Data that showed a decrease after initial large increase, were excluded. The small share of ebullition may be a peculiarity of our long chamber closing time of 1 hour.
Line 106: Treating non-detectable fluxes as zeroes (rather than as a “n/a” or flux at the limit of detection) is a judgement call, given that there is a line of reasoning which argues that treating these data as zeroes biases your dataset towards zero values, when in fact these data points may be producing/consuming gases below the limit of detection. I recommend that the authors provide some justification for this judgement call, given that this is a non-trivial decision.
This concerns only the N2O measurements, as we did not set any CO2 or CH4 measurements to 0. We set 32 out of the 165 N2O datapoints to 0, mostly among small fluxes or faulty chambers. Excluding them would bias the data towards larger fluxes while low microbial activity under unfavourable environmental conditions is a perfectly reasonable assumption. We will explain this in the Material and Methods section.
Line 116 and line 128: It is important to recognise that storage of tropical soils at low temperatures can negatively influence soil microbial communities and microbial activity, given that tropical microorganisms are not cold-adapted and can be severely impacted by storage at sub-ambient temperatures. There is quite a long history of research on this topic, and I recommend that the authors familiarise themselves with the peer-reviewed literature on this topic. The search string “cold storage tropical soil microbial activity” in Google Scholar produces at least half a dozen relevant references, including historic papers by Verchot (1999) Soil Sci Soc Am J and Arnold et al. (2008) Soil Bio Biochem on the effects of cold storage on N cycling in in tropical soils.
That would concern only the denitrification potentials, as we carried the rest of the microbial-activity dependent analyses out in the field. The N2 potential in the Swamp measurements was high in September compared to the other, dry sites but it was modest compared to the long-inundated March samples with low N2O emissions. Thus, the incubations showed various denitrification rates unrelated to sampling time but only related to their ambient environmental conditions.
Line 201: Mention of DNDC at this point in the narrative comes from left-field, since DNDC and modelling were not discussed before this. It’s not clear from the narrative if the authors used DNDC in their research or if they are drawing on findings from modelling studies to interpret their findings. This needs to be clarified as it is confusing.
Mentioning DNDC only gives broader context of the usability of rainfall event data for predicting N2O hot moments. However, if it feels out of context, we will remove the statement.
Lines 251-255: Given the small geographical and temporal scope of this study, I think that the authors are over-reaching when they upscale their fluxes to the entire basin. While these kinds of back of the envelope exercises are interesting and important for progressing the discussion, I think the authors need to be more circumspect about the claims they are making. In this instance, I recommend that the authors revise these sentence construction to make it clear that these numbers are highly speculative and represent first order estimates to gauge relative importance. To be clear, I’m not necessarily saying that the authors should remove these calculations, but rather they should change the language so it’s clear that there estimates are a speculative exercise, rather than certain predictions of the emissions potential of the basin.
We will remove the upscaling results from the text.
Lines 147-261: With respect to reporting fluxes in the body of the text, and I recommend that the authors make it clear when they are referring to field data or incubation data, given that results from laboratory incubations are often not directly comparable to field measurements because of differences in measurement scale, methodology, different handling/treatment effects, and problems of comparing open system (field) versus closed system (laboratory) measurements. The paper as it is currently written doesn’t clearly distinguish between data from these two different types of studies.
We refer to ‘potential’ only where we report incubations. We will clarify that in paragraph LL 228–236.
Citation: https://doi.org/10.5194/bg-2021-46-AC1
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RC2: 'Comment on bg-2021-46', Anonymous Referee #2, 21 Jun 2021
I have now reviewed ‘High greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon’ by Pärn et al.
This study discusses results from monitoring GHG in peatlands under various land-use systems, in the Peruvian Amazon. The issue that is raised in the paper is important and timely. Anthropogenic pressure is increasingly threatening natural peatland systems, with potential important outcomes for the regional C and GHG balance.
However, I’m left a bit disappointed after having read the paper. There are too many issues and unclarities to recommend this paper for publication. And I must say that I have not enough information to assess the scientific validity of the version (see the major issues below). In my opinion, this paper needs to be rewritten to be acceptable anywhere. I have tried to give a list of ‘constructive’ comments below, which might help in this process. Important, and a bit less constructive I’m afraid, is that the dataset will remain limited. To me, it seems more like an exploratory dataset that could go in a proposal for more detailed work on this, or for a kind of perspectives piece somewhere, rather than a full research article. You cannot really go to comparing the anthropogenic impact on full GHG balances with only two systems (I don’t consider the slope site as included, only two days of measurements – we have to draw the line somewhere…), with minimal data (a handful of measurements, during half of a hydrological year, mainly confined in one season?). You also cannot really go to mechanisms, since the in-depth work is missing a bit…
The study sites are not well enough described for an informed reader to understand:
- I work on GHG balances of tropical ecosystems, but not specifically in peatland complexes. However, I did not understand the seasonality (or lack thereof) of inundation, or how the disturbed systems were drained (or not) before they were planted with agricultural crops. This really impedes the understanding of this paper, even for readers with interest and expertise in this topic. For me as a reviewer: you measured only from September to March (approx.. half a year) – it is unclear whether this encompasses a certain season, and whether your upscaling to a year makes sense. I actually looked up the seasonality myself: you monitored the rainy season if I’m correct? Than why not the dry season as well? And how would that affect your conclusions??
- Additionally, you write in L 85: “on the slope and manioc sites, we installed three toposequent stations … “. Some more info is needed here: what was the exact setup. And moreover: what with the forest sites? No toposequent stations? So how was the setup there, then?
Other major issues
- The build-up and communication of the key message of the manuscript is problematic. The introduction actually shows this well: 1) Peatlands are important C stocks, 2) tropical peatlands vulnerable, 3) tropical peatlands are vulnerable, 4) very important for N2O, 5) diving into the mechanistics behind the N2O, 6) Amazon basin important for N2O globally, 7) again mechanistics in peatland N2O, then ending the paragraph with ‘Brazil is also a major contributor to the global increase in N2O emissions during the last decades, owing to the increase in N fertilization’. Then the next paragraph you continue suddenly on the C sequestration in the peat GHG balance. You go on about microbial C respiration and conclude than that drought-induced tree mortality is saturating the Amazon C sink. The tree dieback described in Hubau et al. (earlier shown by Brienen et al. in 2015) has nothing to do with a positive feedback loop of microbes that acclimatize to rising temperature. Also the link with this ‘drying’ of forests themselves through el nino effects and then your ‘human disturbance’ is not clear to me. Do you want to look at climate change effects on the peatland forests, or do you want to focus on the effects of converting forests to agricultural fields? Not clear. While many of the statements might be factually correct, it doesn’t necessarily set out a comprehensible intro for the reader.
- Your end of your intro sets out the objectives: to fill the knowledge gap and to identify environmental drivers of GHG fluxes across gradients of land use and water table. I don’t see this reflected in the set up: if we forget about the slope site (only two measurement days), you only have two systems, so we can hardly call this a gradient. It is completely unclear how comparable they are in there topographic setting: is the disturbed field like the forest site, but then converted? Is the water table at the same level in both? Furthermore: how don’t really identify the environmental drivers at play, right? You just measured all of them, but did not really quantify the importance of one vs. the others in governing the GHG balance? It’s more that you look at some bivariate correlations and explain those, rather than to work with the full set of explanatories you have at hand.
- I’m in general not against having a joint ‘results and discussion’ section, but in this case it becomes all very unclear. One (out of many) examples: in L154 you write ‘that nutrients may have enhanced heterotrophic CO2 and N2O production’, while at this point you did not report anything about the fluxes themselves yet.
- The language needs to improve, see some specific examples below.
Methodological unclarities:
- You installed the collars: but it is unclear whether these were installed once, and then re-used throughout the monitoring period? Or re-installed every time? Did you allow the collar to ‘equilibrate’ for a couple of days after installation? It has been shown that right after installation you disturb the soil enough to boost mineralization..
- For your He-O2 method: ig will be important here what you use for soil moisture levels in the incubation. You state the ‘flushing depended on the soil moisture’, but I don’t see how you set the moisture level? Did you just take the moisture from the soil as it was sampled? How long between the sampling and the incubation (also important for N depletion etc.).
- Did you overpressurize when transferring the gas samples from the chambers to the 50ml glass vials? Not doing so will likely introduce dilution effects when transferring the sample to the GC…
- How did you ‘observe’ water table height in the observation wells? Just visually?
- L 115: a peat sample was collected from each chamber after the sampling sessions in September and March à do you mean after each session? Does this mean that you reinstalled chambers at every sampling occasion? Cfr. Comment above: then your fluxes would likely be affected by the disturbance of forcing a chamber collar in the soil.
- Slope monitoring: so 4 ‘sampling’ events, clustered on two consecutive days. So basically two days of monitoring. Same day measurements are obviously not independent and temporally autocorrelated (you also need the statistical tools to deal with that in your correlations, correlation and GAM assume independent samples). I’m sorry, but that is really too limited to go to a GHG balance. More general: the monitoring took place on a different amount of days in the three sites, and on different time points. This would be “ok-ish” to go to inter-site comparisons if you would have a lot of measurements, but with the limited sample set, I don’t see how you can scientifically justify these comparisons. Especially not if your manuscript conclusion is ‘Our study shows that even moderate drying in the Peruvian palm swamps may create a devastating feedback on climate change through CO2 and N2O emissions.”. That’s just a dramatic overstating of your data. It’s not even clear what you mean by that: do you mean the agricultural vs. forest site comparison? I guess not, since the N2O and CO2 fluxes are in the same range there? So it must be that you mean the drying of the forest site itself? But I do not see data to support that statement? All unclear to me, after having spent quite some time with this manuscript, and that is not how it’s supposed to be unfortunately.
Some specific comments, but not exhaustive I’m afraid:
- Title: ‘High’ relative to what??
- L19: ‘remove’ large amounts of CO2 -> you make it sound as if the flux into the system is exceptionally high, while it’s my understanding that it’s mainly the stock that is high. So ‘store’ would be better here.
- L27: retaining their high CH4 -> rephrase
- L38: undisturbed peat swamp forests sequester carbon for tens of kyr. Do you mean: have been sequestering carbon for the past millennia?
- L52: unclear: the amazon has an exceptionally high 10% share of nitrification in N2O production. Do you mean that 10% of the produced NO3 is further emitted through N2O?
- L60: a quickly increasing disturbance à not proper English.
- L62: where is your reference for ‘droughts increase ecosystem respiration’? Kind of a general statement as well, no?
- L63: explain what you mean with that positive feedback loop for the reader, please.
- L106: how many datapoints did you set to 0?
- L106: you should add a statement on why you would use a linear, and not a quadratic, fit.
- L165: ‘the dry station’ à do you mean the slope? Not clear: be consistent in your naming of your sites.
- L167: that station represents the optimal soil moisture: you cannot say this. You make a relative comparison here, while optimal would be on an ‘absolute’ basis.
- Figure 6: do you really need to show the P-value until 8 numbers after the decimal?
- L208: when you make a comparative statement like this, it would be good to also give those numbers to the reader. ‘Agreed with huge N2O emissions from floodplains’ à how high where those ‘huge’ fluxes.
- L230: consistently use N2O-N please.
- L213-227 is a long speculation of several potential reasons for the combined observation of low NO3 and low N2O. At line 224 the authors write ‘third’, while this is already the fourth potential reason. This whole section is speculative and can be shortened in my opinion.
- L235: where is the toe-slope?
- L233:manioc field: be consistent in the naming
- L260-261: very strange sentence at this spot.
- L 263: please be consistent in the naming of your different systems. What do you mean with arable peatland? The agricultural fields? Use this throughout the manuscript.
- L266-267: high nitrifier denitrification while suppressing the full denitrification pathway à strange formulation: you show high N2 outgassing in your earlier section?
- Also: you actually don’t show nitrifier denitrification. You list a number of potential mechanisms and many rely on earlier work to say that it is ‘likely’ nitrifier denitrification. You would need tracing or isotopocule data to infer that.
Citation: https://doi.org/10.5194/bg-2021-46-RC2 -
AC2: 'Reply on RC2', Jaan Pärn, 11 Jul 2021
I have now reviewed ‘High greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon’ by Pärn et al.
This study discusses results from monitoring GHG in peatlands under various land-use systems, in the Peruvian Amazon. The issue that is raised in the paper is important and timely. Anthropogenic pressure is increasingly threatening natural peatland systems, with potential important outcomes for the regional C and GHG balance.
Thank you for the thorough review and recognition of importance.
However, I’m left a bit disappointed after having read the paper. There are too many issues and unclarities to recommend this paper for publication. And I must say that I have not enough information to assess the scientific validity of the version (see the major issues below). In my opinion, this paper needs to be rewritten to be acceptable anywhere. I have tried to give a list of ‘constructive’ comments below, which might help in this process.
Thank you for the comments, we will rewrite the MS accordingly.
Important, and a bit less constructive I’m afraid, is that the dataset will remain limited. To me, it seems more like an exploratory dataset that could go in a proposal for more detailed work on this, or for a kind of perspectives piece somewhere, rather than a full research article. You cannot really go to comparing the anthropogenic impact on full GHG balances with only two systems
We acknowledge the limits and the exploratory nature of our dataset. We have not claimed However, we feel that the near-simultaneous comparisons of sites under various land uses, and the hot moment of N2O emission in our observations are important and timely enough to be published in an interactive open-access journal like Biogeosciences. We will certainly tone down the generality of conclusions and try to keep within the limits of our observations.
(I don’t consider the slope site as included, only two days of measurements – we have to draw the line somewhere…)
We agree that the Slope site includes the same number of observations as a subset of the other sites, and thus does not carry the same weight as the other sites. We do not rely on any time-series analysis of the Slope site. We already excluded the Slope site from a number of analyses, such as the one presented in Figure 6. However, as the PC plot (Figure 3) shows, the Slope site sits between the Swamp and Manioc sites as expected. Within the site, soil respiration follows the water table depth, as expected. Thus, it is fair to say that despite the low number of measurements and a lack of a dimension of time, the site, rather than creating erratic noise, complements the land use gradient from a pristine swamp to an intensively used agricultural field.
with minimal data (a handful of measurements
We agree that the data are insufficient for annual GHG budgets, and we will remove all statements implying those.
during half of a hydrological year, mainly confined in one season?).
We did not time our study period to any season, nor can it be confined in a single season. The start of our study period in September 2019 is most accurately described as the end of the dry season. However, the ensuing rains only lasted up until late December. The area received hardly any rain from January till March. We do agree that an annual upscaling of GHG fluxes from this rather atypical weather is a stretch. We will remove the results of the upscaling.
You also cannot really go to mechanisms, since the in-depth work is missing a bit…
Indeed, we cannot exclusively identify nitrifier denitrification as the mechanism of N2O production. Therefore, we agree to remove the statement from the Abstract and Conclusions. However, the absence of nitrate still rules out denitrification and nitrification leaving nitrifier denitrification as the only candidate mechanism that directly produces N2O in the soil. Moreover, as Hergoualc’h et al. (2020) identified nitrifier denitrification as the main N2O production mechanism in the site before, we feel that the discussion in lines 211–226 is justified.
The study sites are not well enough described for an informed reader to understand:
We will be happy to elaborate the study site description.
- I work on GHG balances of tropical ecosystems, but not specifically in peatland complexes. However, I did not understand the seasonality (or lack thereof) of inundation
As explained above, it would be confusing to explain seasonality in this study period. The start of our study period in September 2019 is most accurately described as the end of the dry season. The ensuing rains raised the water table to the ground level but only lasted up until late December. The area received hardly any rain from January till March, during which the water table remained close to the ground level. We will include the water table dynamic in the site description.
how the disturbed systems were drained (or not) before they were planted with agricultural crops. This really impedes the understanding of this paper, even for readers with interest and expertise in this topic.
The Slope and Manioc sites were not ditch-drained. The main factors that effected their drying were their location on slopes, the slash and burn of forest and conventional hand-hoe tillage. We will provide information on the land-use history in the site description.
For me as a reviewer: you measured only from September to March (approx.. half a year) – it is unclear whether this encompasses a certain season
The start of our study period in September 2019 is most accurately described as the end of the dry season. The ensuing rains raised the water table to the ground level but only lasted up until late December. The area received hardly any rain from January till March, during which the water table remained close to the ground level. We will include the water table dynamic in the site description.
whether your upscaling to a year makes sense.
The idea of the upscaling was to put our numbers into the context of the extent of peatland area potentially under threat. Indeed, the study period did not cover typical seasonality, but it did involve broadly the same alteration between showers and dryness as a normal year in the area. As a bottom line, we propose to remove the results of the upscaling from the manuscript and find other ways to provide context for the results.
I actually looked up the seasonality myself: you monitored the rainy season if I’m correct?
September to March would be a rainy season in a normal year, but hardly any rain fell from January till March. Therefore, it would be misleading to call it a typical rainy season for the Peruvian Amazon.
Than why not the dry season as well? And how would that affect your conclusions??
We did not design our study to represent a typical or any year. A main assumption of our study was that the GHG result from the immediate environmental conditions. Thus, apart from issues with the upscaling, our conclusions remain valid.
- Additionally, you write in L 85: “on the slope and manioc sites, we installed three toposequent stations … “. Some more info is needed here: what was the exact setup.
We will provide landscape profiles to the study site description section.
And moreover: what with the forest sites? No toposequent stations? So how was the setup there, then?
The Swamp site was located in perfectly flat terrain. We established the chambers in no particular sequence to any topographic features. We will declare that in the site description.
Other major issues
The build-up and communication of the key message of the manuscript is problematic. The introduction actually shows this well: 1) Peatlands are important C stocks, 2) tropical peatlands vulnerable, 3) tropical peatlands are vulnerable, 4) very important for N2O, 5) diving into the mechanistics behind the N2O, 6) Amazon basin important for N2O globally, 7) again mechanistics in peatland N2O, then ending the paragraph with ‘Brazil is also a major contributor to the global increase in N2O emissions during the last decades, owing to the increase in N fertilization’. Then the next paragraph you continue suddenly on the C sequestration in the peat GHG balance. You go on about microbial C respiration and conclude than that drought-induced tree mortality is saturating the Amazon C sink. The tree dieback described in Hubau et al. (earlier shown by Brienen et al. in 2015) has nothing to do with a positive feedback loop of microbes that acclimatize to rising temperature. Also the link with this ‘drying’ of forests themselves through el nino effects and then your ‘human disturbance’ is not clear to me. Do you want to look at climate change effects on the peatland forests, or do you want to focus on the effects of converting forests to agricultural fields? Not clear. While many of the statements might be factually correct, it doesn’t necessarily set out a comprehensible intro for the reader.
Thank you for pointing out the inconsistencies in the text! We will order the statements more logically and remove the ones not directly relevant to the main points of the paper.
- Your end of your intro sets out the objectives: to fill the knowledge gap and to identify environmental drivers of GHG fluxes across gradients of land use and water table. I don’t see this reflected in the set up: if we forget about the slope site (only two measurement days), you only have two systems, so we can hardly call this a gradient. It is completely unclear how comparable they are in there topographic setting: is the disturbed field like the forest site, but then converted?
Generally – yes, both are on a peaty soil and practically every aspect of ecological difference between the two sites is caused by the slashing of forest, burning and agricultural use. We will describe the land use history in the study site section.
Is the water table at the same level in both?
As the extremely different soil water contents (0.8 m3 m–3 vs 0.15 m3 m–3) indicate, the water table was close to the ground in the Swamp site while it was about 1.5m below the ground in the Manioc site. Before the slash-and-burn agriculture, the water table was, on average, at the same level
Furthermore: how don’t really identify the environmental drivers at play, right? You just measured all of them, but did not really quantify the importance of one vs. the others in governing the GHG balance? It’s more that you look at some bivariate correlations and explain those, rather than to work with the full set of explanatories you have at hand.
We did test the correlations between the greenhouse gas fluxes and all environmental characteristics, both within and across the sites. We only displayed the significant correlations and, to tighten the communication, we did not display the insignificant correlations. However, to quantify the relative importance of the significant correlations, it is probably best to show the correlation matrices.
- I’m in general not against having a joint ‘results and discussion’ section, but in this case it becomes all very unclear. One (out of many) examples: in L154 you write ‘that nutrients may have enhanced heterotrophic CO2 and N2O production’, while at this point you did not report anything about the fluxes themselves yet.
We agree to move the discussion to a separate section.
- The language needs to improve, see some specific examples below.
We will ask a native English-speaking editor to proofread the manuscript.
Methodological unclarities:
- You installed the collars: but it is unclear whether these were installed once, and then re-used throughout the monitoring period? Or re-installed every time? Did you allow the collar to ‘equilibrate’ for a couple of days after installation? It has been shown that right after installation you disturb the soil enough to boost mineralization..
We installed the collars twice: early September and early January, and allowed a stabilisation time of several days before the sampling. We will specify this in the Methods section.
- For your He-O2 method: ig will be important here what you use for soil moisture levels in the incubation. You state the ‘flushing depended on the soil moisture’, but I don’t see how you set the moisture level? Did you just take the moisture from the soil as it was sampled?
Our statement ’The flushing time depended on the soil moisture.’ is just an a posteriori observation on how long it took to establish the new equilibrium in the intact soil core, i.e. to replace the air inside (mostly containing N2) with the artificial gas mixture. Therefore, we did not set the moisture level, we just replaced the soil air and report that the flushing time was longer in the wetter soils.
How long between the sampling and the incubation (also important for N depletion etc.).
Transport and storage time after the sampling was approximately a week.
- Did you overpressurize when transferring the gas samples from the chambers to the 50ml glass vials? Not doing so will likely introduce dilution effects when transferring the sample to the GC…
We did not overpressurise but our GC system does is fully sealed and under vacuum, thus excluding any dilution with lab air. The GC demand of gas is 25–30ml, which is half the volume of our 50ml sample. The vacuum pulls the gas sample into the sealed system.
- How did you ‘observe’ water table height in the observation wells? Just visually?
We observed water table height using a tape measure. We will specify this in the Material and Methods section.
- L 115: a peat sample was collected from each chamber after the sampling sessions in September and March à do you mean after each session? Does this mean that you reinstalled chambers at every sampling occasion? Cfr. Comment above: then your fluxes would likely be affected by the disturbance of forcing a chamber collar in the soil.
As we state in the Material and Methods section, we collected soil twice: “A peat sample of 150 to 200 g was collected from each chamber between 0 to 0.1 m depth after the sampling sessions in September and March.” We installed the collars twice: early September and early January, and allowed a stabilisation time of several days before the gas sampling. We will specify this in the Material and Methods section.
- Slope monitoring: so 4 ‘sampling’ events, clustered on two consecutive days. So basically two days of monitoring. Same day measurements are obviously not independent and temporally autocorrelated (you also need the statistical tools to deal with that in your correlations, correlation and GAM assume independent samples). I’m sorry, but that is really too limited to go to a GHG balance. More general: the monitoring took place on a different amount of days in the three sites, and on different time points. This would be “ok-ish” to go to inter-site comparisons if you would have a lot of measurements, but with the limited sample set, I don’t see how you can scientifically justify these comparisons.
Thank you for the critical evaluation of our Slope sample. Not sure, though, whether the gas samples from the same site on different months are statistically independent from each other and whether that is an essential problem. We acknowledge that the monitoring of the Slope site was short, and the data can only be used to compare with subsamples of similar extent, such as the September observations of the Swamp and Manioc sites (like in Fig. 7).
- Especially not if your manuscript conclusion is ‘Our study shows that even moderate drying in the Peruvian palm swamps may create a devastating feedback on climate change through CO2 and N2O emissions.”. That’s just a dramatic overstating of your data.
We agree that this statement tried to summarise too many results into one general statement. We will remove this statement and add sentences that are more directly limited with our results.
- It’s not even clear what you mean by that: do you mean the agricultural vs. forest site comparison? I guess not, since the N2O and CO2 fluxes are in the same range there? So it must be that you mean the drying of the forest site itself? But I do not see data to support that statement? All unclear to me, after having spent quite some time with this manuscript, and that is not how it’s supposed to be unfortunately.
This statement encompassed two observations: 1) The Manioc field retained high CO2 and N2O emissions after the conversion (which itself caused high but unmeasured CO2 emissions from burning, and prevented CO2 sequestration in trees); 2) We link the high CO2 and N2O emissions from the Swamp forest with the seasonal water table drawdown. We agree that the points can be communicated better and will try to break them down better.
Some specific comments, but not exhaustive I’m afraid:
- Title: ‘High’ relative to what??
Substantial comment. What we meant is high relative to sequestration or zero balance. However, probably it is better to remove this adjective from the title.
- L19: ‘remove’ large amounts of CO2 -> you make it sound as if the flux into the system is exceptionally high, while it’s my understanding that it’s mainly the stock that is high. So ‘store’ would be better here.
Agreed.
- L27: retaining their high CH4 -> rephrase
Agreed.
- L38: undisturbed peat swamp forests sequester carbon for tens of kyr. Do you mean: have been sequestering carbon for the past millennia?
We mean thousands of years but the policy of Biogeosciences is not to use words for numbers but to use k for thousands. However, if that is misleading, we will be glad to use millennia instead.
- L52: unclear: the amazon has an exceptionally high 10% share of nitrification in N2O production. Do you mean that 10% of the produced NO3 is further emitted through N2O?
The ‘high 10% share of nitrification in N2O production’ means 10% of the N2O is produced in nitrification. Denitrification and other processes are responsible for the 90%. However, it may be that this point is too specific for the introduction.
- L60: a quickly increasing disturbance à not proper English.
We will let a native-speaking editor to proofread the manuscript.
- L62: where is your reference for ‘droughts increase ecosystem respiration’? Kind of a general statement as well, no?
For us, the fact that soil drying and warming increase ecosystem respiration is textbook material. We will cite a reference for that.
- L63: explain what you mean with that positive feedback loop for the reader, please.
Agreed.
- L106: how many datapoints did you set to 0
We set 32 out of the 165 N2O datapoints to 0. We did not set any CO2 or CH4 datapoints to 0. We will include the information in the Material and Methods section.
- L106: you should add a statement on why you would use a linear, and not a quadratic, fit.
Agreed. The linear fit is the only one that does not assume either saturation or quasi-exponential rise in concentration.
- L165: ‘the dry station’ à do you mean the slope? Not clear: be consistent in your naming of your sites.
‘The dry station (water table –0.7 m; soil water content 0.26 m3 m–3; soil temperature around 26 ºC at 10 cm depth) of the young swamp forest’ is the dry station of the Slope site. We will correct that.
- L167: that station represents the optimal soil moisture: you cannot say this. You make a relative comparison here, while optimal would be on an ‘absolute’ basis.
The point here is that we observed the highest soil respiration at this moisture, not the driest one.
- Figure 6: do you really need to show the P-value until 8 numbers after the decimal?
We can just state ‘p<0.01’ but not sure whether that would convey the same information.
- L208: when you make a comparative statement like this, it would be good to also give those numbers to the reader. ‘Agreed with huge N2O emissions from floodplains’ à how high where those ‘huge’ fluxes.
We will provide the figures from the earlier papers.
- L230: consistently use N2O-N please.
Will do that.
- L213-227 is a long speculation of several potential reasons for the combined observation of low NO3 and low N2O. At line 224 the authors write ‘third’, while this is already the fourth potential reason. This whole section is speculative and can be shortened in my opinion.
Agreed. We will shorten that paragraph.
- L235: where is the toe-slope?
We will specify that.
- L233:manioc field: be consistent in the naming
Agreed.
- L260-261: very strange sentence at this spot.
We will remove it.
- L 263: please be consistent in the naming of your different systems. What do you mean with arable peatland? The agricultural fields? Use this throughout the manuscript.
Agreed.
- L266-267: high nitrifier denitrification while suppressing the full denitrification pathway à strange formulation: you show high N2 outgassing in your earlier section?
N2O is the intermediate product of denitrification. High N2O emission with high denitrification potential itself is evidence of incomplete denitrification. The N2 potential in the Swamp measurements was high in September compared to the other, dry sites but it was modest compared to the long-inundated March samples with low N2O emissions.
- Also: you actually don’t show nitrifier denitrification. You list a number of potential mechanisms and many rely on earlier work to say that it is ‘likely’ nitrifier denitrification. You would need tracing or isotopocule data to infer that.
A fair point. We agree to remove the statement from the Abstract and Conclusions and shorten the discussion in lines 211–226. However, the absence of nitrate still rules out denitrification and nitrification leaving nitrifier denitrification as the only candidate mechanism that directly produces N2O in the soil. In addition, Hergoualc’h et al. (2020) identified nitrifier denitrification as the main N2O production mechanism in the site. Therefore, we will keep nitrifier denitrification in the discussion in lines 211–226.
Citation: https://doi.org/10.5194/bg-2021-46-AC2
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RC3: 'Comment on bg-2021-46', Anonymous Referee #3, 03 Aug 2021
PaÌrn et al., 2021 report greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon. The investigated peatland sites covered (1) a slash-and-burn manioc field, (2) a 12-year-old secondary forest grown over a fallow pasture and a banana plantation, and (3) a natural swamp forest. While I very much acknowledge the scientific effort of data collection from a strongly understudied region of the world, I am afraid that the manuscript suffers in its current form from insufficient structural and scientific quality. This is a pity, since the additional laboratory analyses to quantify N2 potential from soil cores from the studied sites are novel and interesting.
Generally, the introduction is weak and does not clearly introduce why studying greenhouse gases from peatlands under various disturbances is important. The introduction mentions nowhere methane which is probably the most important greenhouse gas in these ecosystems and only a couple of lines are spent on carbon dioxide. Moreover, the data coverage is poor; Only 9 sampling sessions, over a period of 7 months (Sept 2019 to March 2020) were conducted at two sites (swamp forest; manioc field) and only four sessions during two consecutive days in Sept 2020 were conducted at the remaining secondary forest site. The reader is left with no explanation on why this irregular sampling strategy was chosen. Lastly, the discussion section does not contextualize the findings with other scientific literature, especially the aspect of disturbance. The word disturbance does not even appear in the discussion. Again, methane as an important greenhouse gas in these ecosystems is barely discussed. Given these substantial drawbacks of the study I recommend rejection of the paper in its current form.
Specific comments:
Abstract
General: The Abstract suffers from vague statements and needs to be more concise.
Line 22: Which ‘changes’? Land-use? Climate?
Line 25: At which frequency?
Line 26: moderate compared to? Give concrete flux numbers.
Line 27: ‘slight water table drawdown’. Pls be more specific. From inundated conditions? How much is ‘slight’
Line 29: ‘Nitrifier-denitrification was the likely source mechanism’ based on which underlying data? This is too speculative.
Introduction:
Line 42-45: How do these numbers relate to each other? Does that mean that these peatlands are a hotspot within the Amazon rainforest hotspot?
Line 54: This sentence is out of context.
Line 59: There is no transition to the C cycle and related CO2 emissions.
Line 62: Can you give a reference for this statement. Drought first and foremost reduces photosynthesis and consequently less assimilates are available for autotrophic and heterotrophic respiration.
Line 65: consider a better transition to the soil part of the intoduction
Materials and Methods:
General: No structuring into subsections
Line 76: suggest renaming site to ‘Swamp primary forest’
Line 76: suggest renaming site to ‘Swamp secondary forest’
Figure 2: what is the Pastaza-MaranÌon Basin? This should be mentioned in the text as well.
Line 85: How many chambers were installed at the swamp site?
Line 85: stations? Why not calling them plots?
Line 86: How long before gas sampling where the collars installed?
Line 92: How much gas was sampled and how? With a syringe and needle through a septum?
Line 100: How was CO2 measured? How was the GC calibrated?
Line 104: How much of the data was affected by this quality check?
Line 128: A ~7cm by 6cm soil core is not very representative.
Line 137: How were the samples taken from the continuously flushed vessel?
Line 137: How was this done exactly? N2 is not easy to measure. How was the GC calibrated?
Line 138: Give equation.
Results and Discussion
Line 154-159: Can the water table change be illustrated graphically along with the actual fluxes of CO2, CH4, and N2O?
Line 155: ‘slope forest’ is not the same site name as specified in the methods. Same for ‘palm swamp’.
Line 165: dry station? I assume the authors refer to the toposequent stations? This needs to be clarified in the method section. Line 166: which site is the ‘young swamp forest’?
Line 167: Why does the dry station represent the optimal moisture for soil respiration?
Line 172: Which site is the swamp peat?
Figure 4: Not been referred to in the text. I guess this should be done in line 173.
Figure 5: Why not CO2 flux instead of soil respiration. That would be more in line with the other fluxes.
Line 176: I assume the authors refer to the eddy covariance technique.
Line 180: prevail --> dominate
Line 188-194: 6 lines of discussion for CH4 only. This needs to be extended.
Line 195-198: Sudden switch to N2O fluxes with mentioning of soil respiration. Hard to follow the discussion.
Line 200: From what do the authors conclude at this point that N2O was produced from NH4?
Line 211-227: Very speculative paragraph.
Line 235: toe-slope swamp forest? Same as site ‘slope’?
Line 238: Are there any other papers which investigate N2O reduction to N2 in tropical systems? What are the implications for the N cycle?
L251: Upscaling paragraph lacks info on CH4.
Citation: https://doi.org/10.5194/bg-2021-46-RC3 -
AC3: 'Reply on RC3', Jaan Pärn, 23 Aug 2021
Pärn et al., 2021 report greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon. The investigated peatland sites covered (1) a slash-and-burn manioc field, (2) a 12-year-old secondary forest grown over a fallow pasture and a banana plantation, and (3) a natural swamp forest. While I very much acknowledge the scientific effort of data collection from a strongly understudied region of the world, I am afraid that the manuscript suffers in its current form from insufficient structural and scientific quality. This is a pity, since the additional laboratory analyses to quantify N2 potential from soil cores from the studied sites are novel and interesting.
Generally, the introduction is weak and does not clearly introduce why studying greenhouse gases from peatlands under various disturbances is important. The introduction mentions nowhere methane which is probably the most important greenhouse gas in these ecosystems and only a couple of lines are spent on carbon dioxide. Moreover, the data coverage is poor; Only 9 sampling sessions, over a period of 7 months (Sept 2019 to March 2020) were conducted at two sites (swamp forest; manioc field) and only four sessions during two consecutive days in Sept 2020 were conducted at the remaining secondary forest site. The reader is left with no explanation on why this irregular sampling strategy was chosen. Lastly, the discussion section does not contextualize the findings with other scientific literature, especially the aspect of disturbance. The word disturbance does not even appear in the discussion. Again, methane as an important greenhouse gas in these ecosystems is barely discussed. Given these substantial drawbacks of the study I recommend rejection of the paper in its current form.
Thank you for the thorough and fair comment. We will take the points forward and improve the manuscript accordingly. Indeed, we took the importance of GHG from various disturbances in the tropics for granted to the reader of the journal. We tried to keep the introduction brief and summary at the expense of widely known detail on methane and carbon dioxide fluxes. We also spared the reader from technical details on sampling strategy planning. We also agree on the reviewer’s criticism on the underuse of the general concept of disturbance. We believe the manuscript will substantially benefit from expansion on these points and will be glad to improve on them.
Specific comments:
Abstract
General: The Abstract suffers from vague statements and needs to be more concise.
Agreed. We will remove all statements that are vaguely connected to the main discussion.
Line 22: Which ‘changes’? Land-use? Climate?
The statement referred to the changes mentioned in the couple of statements above – drought, cultivation and other changes contributing towards the varying oxygen content. However, we will remove this vague statement.
Line 25: At which frequency?
We will detail the frequency here.
Line 26: moderate compared to? Give concrete flux numbers.
Agreed. We will provide the information.
Line 27: ‘slight water table drawdown’. Pls be more specific. From inundated conditions? How much is ‘slight’.
Good point. We will provide the change in water table in cm from the inundated level.
Line 29: ‘Nitrifier-denitrification was the likely source mechanism’ based on which underlying data? This is too speculative.
Indeed, we cannot exclusively identify nitrifier denitrification as the mechanism of N2O production. Therefore, we agree to remove the statement from the Abstract and Conclusions. However, the absence of nitrate still rules out denitrification and nitrification leaving nitrifier denitrification as the only candidate mechanism that directly produces N2O in the soil. Moreover, as Hergoualc’h et al. (2020) identified nitrifier denitrification as the main N2O production mechanism in the site before, we feel that the discussion in lines 211–226 is justified.
Introduction:
Line 42-45: How do these numbers relate to each other? Does that mean that these peatlands are a hotspot within the Amazon rainforest hotspot?
Yes, the Peruvian peatlands are a potential contributor within the larger Amazonian hotspot, and we will alter the sentence to state that.
Line 54: This sentence is out of context.
True. The statement needs a transition sentence.
Line 59: There is no transition to the C cycle and related CO2 emissions.
We intended this paragraph as a summary of all three GHGs. However, we take the point that in this form it may be misleading to the C fluxes again. We will restructure the Introduction section for a more logical order.
Line 62: Can you give a reference for this statement. Drought first and foremost reduces photosynthesis and consequently less assimilates are available for autotrophic and heterotrophic respiration.
A FLUXNET synthesis (Schwalm et al. 2010 Global Change Biology) should do the job.
Line 65: consider a better transition to the soil part of the introduction
Agreed.
Materials and Methods:
General: No structuring into subsections
Indeed, we did not structure this section into subsections like we did not anywhere else. However, we will consider the structuring here.
Line 76: suggest renaming site to ‘Swamp primary forest’
Line 76: suggest renaming site to ‘Swamp secondary forest’
The correct order of words would probably be ‘Primary swamp forest’ and ‘Secondary swamp forest’. Otherwise, we agree.
Figure 2: what is the Pastaza-MaranÌon Basin? This should be mentioned in the text as well.
Agreed. We will define the basin in the text.
Line 85: How many chambers were installed at the swamp site?
The number is 10. We will state that in the text.
Line 85: stations? Why not calling them plots?
The even more correct name is ‘point’. We will change that throughout the text.
Line 86: How long before gas sampling where the collars installed?
We allowed a stabilisation time of several days before the sampling. We will specify this in the Methods section.
Line 92: How much gas was sampled and how? With a syringe and needle through a septum?
We sampled the gas through tubes and medical three-way taps straight into 50mL vials. We will specify this in the Methods section.
Line 100: How was CO2 measured? How was the GC calibrated?
We determined CO2 concentration with the same flame ionisation detector. We will specify the calibration in the text.
Line 104: How much of the data was affected by this quality check?
We set 32 out of the 165 N2O datapoints to 0. We did not set any CO2 or CH4 datapoints to 0. We will include the information in the Material and Methods section.
Line 128: A ~7cm by 6cm soil core is not very representative.
It is representative of the 50cm diameter collar. We sampled a soil core from each collar.
Line 137: How were the samples taken from the continuously flushed vessel?
Through a tube reaching the headspace through a hermetic septum.
Line 137: How was this done exactly? N2 is not easy to measure. How was the GC calibrated?
We detected N2 concentration on the same analyser as N2O. N2 concentration is not more difficult to measure than N2O (at least we have not seen it stated in literature as such). N2 flux is difficult to measure, but we solved this with the intact soil core technique. We will provide detail on the N2 concentration detection and its calibration.
Line 138: Give equation.
Will do that.
Results and Discussion
Line 154-159: Can the water table change be illustrated graphically along with the actual fluxes of CO2, CH4, and N2O?
Yes, we will do that.
Line 155: ‘slope forest’ is not the same site name as specified in the methods. Same for ‘palm swamp’.
We will change the text for consistency in the site names.
Line 165: dry station? I assume the authors refer to the toposequent stations? This needs to be clarified in the method section.
We will name the toposequent transect points in the Methods section.
Line 166: which site is the ‘young swamp forest’?
This is the Slope site. We will change the statement consistency in the site names.
Line 167: Why does the dry station represent the optimal moisture for soil respiration?
Both dryness and wetness (lack of soil oxygen) may curb soil respiration. The dry point had intermediate soil moisture and showed the highest respiration rates.
Line 172: Which site is the swamp peat?
It is “The Swamp peat …”. We defined the sites in lines 76–78. According to that, the Swamp was “a natural forest in the Quistococha lake floodplain”.
Figure 4: Not been referred to in the text. I guess this should be done in line 173.
We will correct that.
Figure 5: Why not CO2 flux instead of soil respiration. That would be more in line with the other fluxes.
‘CO2 flux’ would be wrong as our opaque chambers exclude photosynthesis and only represent soil respiration.
Line 176: I assume the authors refer to the eddy covariance technique.
Yes, will specify that.
Line 180: prevail --> dominate
We will change that.
Line 188-194: 6 lines of discussion for CH4 only. This needs to be extended.
We will do that.
Line 195-198: Sudden switch to N2O fluxes with mentioning of soil respiration. Hard to follow the discussion.
The switch follows a paragraph break, so it is hardly more sudden than the switch from CO2 to CH4. However, we should probably emphasise the paragraph break more. The surge in soil respiration caused by the water-table drawdown should probably be introduced in the CO2 paragraph.
Line 200: From what do the authors conclude at this point that N2O was produced from NH4?
We stated in line 149: “The waterlogged swamp peat did not contain a detectable amount of NO3–.” This leaves only NH4 and its non-NO3 products as potential sources of N2O.
Line 211-227: Very speculative paragraph.
Not sure what would be a more adequate discussion of the N2O fluxes, soil NH4, NO3, water and O2 content measurements and candidate mechanisms behind the N2O fluxes listed in the literature, including earlier corroborating studies at the same site.
Line 235: toe-slope swamp forest? Same as site ‘slope’?
Yes. We will standardise the site naming throughout the text.
Line 238: Are there any other papers which investigate N2O reduction to N2 in tropical systems? What are the implications for the N cycle?
No, to our knowledge not. We state the main implication for the N cycle in line 241: “Thus, the N2O likely produced from nitrifier denitrification in March was consumed by denitrification.”
L251: Upscaling paragraph lacks info on CH4.
Following the suggestions of the other two reviewers, we will remove the upscaling paragraph altogether.
Citation: https://doi.org/10.5194/bg-2021-46-AC3
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AC3: 'Reply on RC3', Jaan Pärn, 23 Aug 2021
Status: closed
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RC1: 'Comment on bg-2021-46', Yit Arn Teh, 25 Mar 2021
GENERAL COMMENTS
This is a topically relevant paper, given how little is known about peatlands in South America, and growing interest in understanding how tropical peatland management worldwide influences regional and global exchanges of greenhouse gases. This paper adds to the growing body of knowledge on the biogeochemistry of South America peatlands, and nicely integrates field-based flux measurements with more process-based laboratory assays. However, while I am broadly supportive of this paper, I think that the paper needs to be revised in order to enhance reader understanding and to acknowledge potential limitations with the experimental methods and design.
First and foremost, given that this study is of limited geographic scope, with data collected over a relatively narrow window of time (i.e. only 6 months of measurements), the authors need to do more to acknowledge that it may be difficult to generalise their findings to larger spatial domains or longer periods of time. For example, I was concerned that the authors were over-reaching when they extrapolated their data over the entire Pastaza-Marañon foreland basin region (see point 10 below).
Second, the authors need to clarify for non-expert readers if their measurements captured both wet and dry seasons (see point 4 below), given that water table depth and other environmental conditions vary substantially between wet and dry seasons, with a strong wet/dry season signal in CH4 and other trace gas emissions detectable not only from Amazon-basin wide studies of atmospheric chemistry and from smaller scale, site level studies of ecosystem gas exchange (e.g. Wilson et al. 2016). Seasonal affects will have ramifications not only for their field data, but could also influence their incubation results, as water table and other environmental conditions will influence the status of the microbial community at the time of soil collection; e.g. soils collected for incubation during the wet season could have a different activity profile or functional composition from the same soils collected during the dry season.
Third, the cold storage of soil for incubations is problematic and could lead to significant treatment effects (point 8). Historic studies by Louis Verchot, Marife Corre, Ed Veldkamp and others have demonstrated adverse impacts on N cycling microbes (relevant to this study given it’s focus on N2O), and many tropical research teams now transport soils at room temperature or conduct laboratory experiments near their field sites to avoid these treatment effects. While potential treatment effects do not invalidate the incubation studies presented here, the authors need to acknowledge the potential issues caused by cold storage and discuss how this may impact their interpretation of the results.
Fourth, on a more technical point, the authors need to clarify how they treated non-linear data and chambers that show potential evidence of ebullition. Fitting linear curves to non-linear data or excluding ebullition data will tend to underestimate flux rates.
Specific comments are provided in the section below.
SPECIFIC COMMENTS
- Lines 70-72: Since this study only investigated a sub-set of land-uses in the region, it would be clearer and more transparent if the authors indicated here which land-use types they focused on in this paper, with a brief justification for why they have concentrated on these land-uses in particular.
- Lines 76-80: For readers unfamiliar with the Roucoux et al. (2013) paper, I recommend expanding the site description for the human-affected sites so it’s clearer how human intervention has altered these study sites.
- Lines 91-93: Please clarify how many samples were collected over a 60 minute period; i.e. 4 time points (0, 20, 40, 60 minutes) or 3 (20, 40, 60 minutes).
- Lines 95-96: Did these sampling campaigns cover both wet and dry seasons? This is not clear - please clarify this in the narrative. Also indicate in Table 1 what season the campaigns were conducted in so it’s clearer if there was even sampling between seasons.
- Lines 101-102: How was CO2 determined? Did the instrument have a methanizer? Also – N2 flux is mentioned in the Results and Discussion section, but it’s not clear how N2 was measured in the field flux measurements – this must be clarified.
- Lines 102-104: How were non-linear data treated or chambers which showed evidence of ebullition (i.e. erratic or very large non-linear changes in concentration)? Were these data discarded or included?
- Line 106: Treating non-detectable fluxes as zeroes (rather than as a “n/a” or flux at the limit of detection) is a judgement call, given that there is a line of reasoning which argues that treating these data as zeroes biases your dataset towards zero values, when in fact these data points may be producing/consuming gases below the limit of detection. I recommend that the authors provide some justification for this judgement call, given that this is a non-trivial decision.
- Line 116 and line 128: It is important to recognise that storage of tropical soils at low temperatures can negatively influence soil microbial communities and microbial activity, given that tropical microorganisms are not cold-adapted and can be severely impacted by storage at sub-ambient temperatures. There is quite a long history of research on this topic, and I recommend that the authors familiarise themselves with the peer-reviewed literature on this topic. The search string “cold storage tropical soil microbial activity” in Google Scholar produces at least half a dozen relevant references, including historic papers by Verchot (1999) Soil Sci Soc Am J and Arnold et al. (2008) Soil Bio Biochem on the effects of cold storage on N cycling in in tropical soils.
- Line 201: Mention of DNDC at this point in the narrative comes from left-field, since DNDC and modelling were not discussed before this. It’s not clear from the narrative if the authors used DNDC in their research or if they are drawing on findings from modelling studies to interpret their findings. This needs to be clarified as it is confusing.
- Lines 251-255: Given the small geographical and temporal scope of this study, I think that the authors are over-reaching when they upscale their fluxes to the entire basin. While these kinds of back of the envelope exercises are interesting and important for progressing the discussion, I think the authors need to be more circumspect about the claims they are making. In this instance, I recommend that the authors revise these sentence construction to make it clear that these numbers are highly speculative and represent first order estimates to gauge relative importance. To be clear, I’m not necessarily saying that the authors should remove these calculations, but rather they should change the language so it’s clear that there estimates are a speculative exercise, rather than certain predictions of the emissions potential of the basin.
- Lines 147-261: With respect to reporting fluxes in the body of the text, and I recommend that the authors make it clear when they are referring to field data or incubation data, given that results from laboratory incubations are often not directly comparable to field measurements because of differences in measurement scale, methodology, different handling/treatment effects, and problems of comparing open system (field) versus closed system (laboratory) measurements. The paper as it is currently written doesn’t clearly distinguish between data from these two different types of studies.
Citation: https://doi.org/10.5194/bg-2021-46-RC1 -
AC1: 'Reply on RC1', Jaan Pärn, 11 Jul 2021
RC1
GENERAL COMMENTS
This is a topically relevant paper, given how little is known about peatlands in South America, and growing interest in understanding how tropical peatland management worldwide influences regional and global exchanges of greenhouse gases. This paper adds to the growing body of knowledge on the biogeochemistry of South America peatlands, and nicely integrates field-based flux measurements with more process-based laboratory assays. However, while I am broadly supportive of this paper, I think that the paper needs to be revised in order to enhance reader understanding and to acknowledge potential limitations with the experimental methods and design.
Thank you for the supportive comment! We will revise the manuscript accordingly.
First and foremost, given that this study is of limited geographic scope, with data collected over a relatively narrow window of time (i.e. only 6 months of measurements), the authors need to do more to acknowledge that it may be difficult to generalise their findings to larger spatial domains or longer periods of time. For example, I was concerned that the authors were over-reaching when they extrapolated their data over the entire Pastaza-Marañon foreland basin region (see point 10 below).
Agreed. We originally intended the upscaling intended as a general guideline to the reader for context of our numbers, not a central point of the paper. We will remove the upscaling.
Second, the authors need to clarify for non-expert readers if their measurements captured both wet and dry seasons (see point 4 below), given that water table depth and other environmental conditions vary substantially between wet and dry seasons, with a strong wet/dry season signal in CH4 and other trace gas emissions detectable not only from Amazon-basin wide studies of atmospheric chemistry and from smaller scale, site level studies of ecosystem gas exchange (e.g. Wilson et al. 2016). Seasonal affects will have ramifications not only for their field data, but could also influence their incubation results, as water table and other environmental conditions will influence the status of the microbial community at the time of soil collection; e.g. soils collected for incubation during the wet season could have a different activity profile or functional composition from the same soils collected during the dry season.
We are wary to attribute any seasons to our measurement time. The start of our study period in September 2019 is most accurately described as the end of the dry season. However, the ensuing rains only lasted up until late December. The area received hardly any rain from January till March. The water table, however, remained high and stable during the January till March observations, due to the buffering effect of the peat and adjacent Lake Quistococha. We assume the microbial community responded to the immediate environmental conditions, not the multi-annual average pattern of seasons.
Third, the cold storage of soil for incubations is problematic and could lead to significant treatment effects (point 8). Historic studies by Louis Verchot, Marife Corre, Ed Veldkamp and others have demonstrated adverse impacts on N cycling microbes (relevant to this study given it’s focus on N2O), and many tropical research teams now transport soils at room temperature or conduct laboratory experiments near their field sites to avoid these treatment effects. While potential treatment effects do not invalidate the incubation studies presented here, the authors need to acknowledge the potential issues caused by cold storage and discuss how this may impact their interpretation of the results.
We will provide information on the transport, storage, and acclimatisation of the intact soil cores in the Material and Methods section. The bottom line is that the incubations showed various denitrification rates unrelated to sampling time but related to their ambient environmental conditions.
Fourth, on a more technical point, the authors need to clarify how they treated non-linear data and chambers that show potential evidence of ebullition. Fitting linear curves to non-linear data or excluding ebullition data will tend to underestimate flux rates.
We closely examined all our gas concentration trends in each individual chambers. Practically all significant deviations from a linear trend were apparently caused by a faulty chamber sealing. We did not observe any signs of ebullition such as jump rises in concentration not followed by a drop in concentration. An unnoticeable share of ebullition may be a peculiarity of our long chamber closing time of 1 hour.
Specific comments are provided in the section below.
SPECIFIC COMMENTS
Lines 70-72: Since this study only investigated a sub-set of land-uses in the region, it would be clearer and more transparent if the authors indicated here which land-use types they focused on in this paper, with a brief justification for why they have concentrated on these land-uses in particular.
We will clarify the targeted land uses better, both here and the Material and Methods section.
Lines 76-80: For readers unfamiliar with the Roucoux et al. (2013) paper, I recommend expanding the site description for the human-affected sites so it’s clearer how human intervention has altered these study sites.
We will expand the site description accordingly.
Lines 91-93: Please clarify how many samples were collected over a 60 minute period; i.e. 4 time points (0, 20, 40, 60 minutes) or 3 (20, 40, 60 minutes).
We will specify that we took a 0-sample at the start of every 1 h session.
Lines 95-96: Did these sampling campaigns cover both wet and dry seasons? This is not clear - please clarify this in the narrative. Also indicate in Table 1 what season the campaigns were conducted in so it’s clearer if there was even sampling between seasons.
See the comment on seasonality in the General Comments.
Lines 101-102: How was CO2 determined? Did the instrument have a methanizer?
The GC-2014 does not have a methaniser. We will specify that CO2 was also determined with the flame ionisation detector.
Also – N2 flux is mentioned in the Results and Discussion section, but it’s not clear how N2 was measured in the field flux measurements – this must be clarified.
The protocol for N2 denitrification potential determination is specified in lines 128–139.
Lines 102-104: How were non-linear data treated or chambers which showed evidence of ebullition (i.e. erratic or very large non-linear changes in concentration)? Were these data discarded or included?
We closely examined all our gas concentration trends in each individual chambers. Practically all significant deviations from a linear trend were apparently caused by a faulty chamber sealing. We did not observe any signs of ebullition such as jump rises in concentration not followed by a drop in concentration. Data that showed a decrease after initial large increase, were excluded. The small share of ebullition may be a peculiarity of our long chamber closing time of 1 hour.
Line 106: Treating non-detectable fluxes as zeroes (rather than as a “n/a” or flux at the limit of detection) is a judgement call, given that there is a line of reasoning which argues that treating these data as zeroes biases your dataset towards zero values, when in fact these data points may be producing/consuming gases below the limit of detection. I recommend that the authors provide some justification for this judgement call, given that this is a non-trivial decision.
This concerns only the N2O measurements, as we did not set any CO2 or CH4 measurements to 0. We set 32 out of the 165 N2O datapoints to 0, mostly among small fluxes or faulty chambers. Excluding them would bias the data towards larger fluxes while low microbial activity under unfavourable environmental conditions is a perfectly reasonable assumption. We will explain this in the Material and Methods section.
Line 116 and line 128: It is important to recognise that storage of tropical soils at low temperatures can negatively influence soil microbial communities and microbial activity, given that tropical microorganisms are not cold-adapted and can be severely impacted by storage at sub-ambient temperatures. There is quite a long history of research on this topic, and I recommend that the authors familiarise themselves with the peer-reviewed literature on this topic. The search string “cold storage tropical soil microbial activity” in Google Scholar produces at least half a dozen relevant references, including historic papers by Verchot (1999) Soil Sci Soc Am J and Arnold et al. (2008) Soil Bio Biochem on the effects of cold storage on N cycling in in tropical soils.
That would concern only the denitrification potentials, as we carried the rest of the microbial-activity dependent analyses out in the field. The N2 potential in the Swamp measurements was high in September compared to the other, dry sites but it was modest compared to the long-inundated March samples with low N2O emissions. Thus, the incubations showed various denitrification rates unrelated to sampling time but only related to their ambient environmental conditions.
Line 201: Mention of DNDC at this point in the narrative comes from left-field, since DNDC and modelling were not discussed before this. It’s not clear from the narrative if the authors used DNDC in their research or if they are drawing on findings from modelling studies to interpret their findings. This needs to be clarified as it is confusing.
Mentioning DNDC only gives broader context of the usability of rainfall event data for predicting N2O hot moments. However, if it feels out of context, we will remove the statement.
Lines 251-255: Given the small geographical and temporal scope of this study, I think that the authors are over-reaching when they upscale their fluxes to the entire basin. While these kinds of back of the envelope exercises are interesting and important for progressing the discussion, I think the authors need to be more circumspect about the claims they are making. In this instance, I recommend that the authors revise these sentence construction to make it clear that these numbers are highly speculative and represent first order estimates to gauge relative importance. To be clear, I’m not necessarily saying that the authors should remove these calculations, but rather they should change the language so it’s clear that there estimates are a speculative exercise, rather than certain predictions of the emissions potential of the basin.
We will remove the upscaling results from the text.
Lines 147-261: With respect to reporting fluxes in the body of the text, and I recommend that the authors make it clear when they are referring to field data or incubation data, given that results from laboratory incubations are often not directly comparable to field measurements because of differences in measurement scale, methodology, different handling/treatment effects, and problems of comparing open system (field) versus closed system (laboratory) measurements. The paper as it is currently written doesn’t clearly distinguish between data from these two different types of studies.
We refer to ‘potential’ only where we report incubations. We will clarify that in paragraph LL 228–236.
Citation: https://doi.org/10.5194/bg-2021-46-AC1
-
RC2: 'Comment on bg-2021-46', Anonymous Referee #2, 21 Jun 2021
I have now reviewed ‘High greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon’ by Pärn et al.
This study discusses results from monitoring GHG in peatlands under various land-use systems, in the Peruvian Amazon. The issue that is raised in the paper is important and timely. Anthropogenic pressure is increasingly threatening natural peatland systems, with potential important outcomes for the regional C and GHG balance.
However, I’m left a bit disappointed after having read the paper. There are too many issues and unclarities to recommend this paper for publication. And I must say that I have not enough information to assess the scientific validity of the version (see the major issues below). In my opinion, this paper needs to be rewritten to be acceptable anywhere. I have tried to give a list of ‘constructive’ comments below, which might help in this process. Important, and a bit less constructive I’m afraid, is that the dataset will remain limited. To me, it seems more like an exploratory dataset that could go in a proposal for more detailed work on this, or for a kind of perspectives piece somewhere, rather than a full research article. You cannot really go to comparing the anthropogenic impact on full GHG balances with only two systems (I don’t consider the slope site as included, only two days of measurements – we have to draw the line somewhere…), with minimal data (a handful of measurements, during half of a hydrological year, mainly confined in one season?). You also cannot really go to mechanisms, since the in-depth work is missing a bit…
The study sites are not well enough described for an informed reader to understand:
- I work on GHG balances of tropical ecosystems, but not specifically in peatland complexes. However, I did not understand the seasonality (or lack thereof) of inundation, or how the disturbed systems were drained (or not) before they were planted with agricultural crops. This really impedes the understanding of this paper, even for readers with interest and expertise in this topic. For me as a reviewer: you measured only from September to March (approx.. half a year) – it is unclear whether this encompasses a certain season, and whether your upscaling to a year makes sense. I actually looked up the seasonality myself: you monitored the rainy season if I’m correct? Than why not the dry season as well? And how would that affect your conclusions??
- Additionally, you write in L 85: “on the slope and manioc sites, we installed three toposequent stations … “. Some more info is needed here: what was the exact setup. And moreover: what with the forest sites? No toposequent stations? So how was the setup there, then?
Other major issues
- The build-up and communication of the key message of the manuscript is problematic. The introduction actually shows this well: 1) Peatlands are important C stocks, 2) tropical peatlands vulnerable, 3) tropical peatlands are vulnerable, 4) very important for N2O, 5) diving into the mechanistics behind the N2O, 6) Amazon basin important for N2O globally, 7) again mechanistics in peatland N2O, then ending the paragraph with ‘Brazil is also a major contributor to the global increase in N2O emissions during the last decades, owing to the increase in N fertilization’. Then the next paragraph you continue suddenly on the C sequestration in the peat GHG balance. You go on about microbial C respiration and conclude than that drought-induced tree mortality is saturating the Amazon C sink. The tree dieback described in Hubau et al. (earlier shown by Brienen et al. in 2015) has nothing to do with a positive feedback loop of microbes that acclimatize to rising temperature. Also the link with this ‘drying’ of forests themselves through el nino effects and then your ‘human disturbance’ is not clear to me. Do you want to look at climate change effects on the peatland forests, or do you want to focus on the effects of converting forests to agricultural fields? Not clear. While many of the statements might be factually correct, it doesn’t necessarily set out a comprehensible intro for the reader.
- Your end of your intro sets out the objectives: to fill the knowledge gap and to identify environmental drivers of GHG fluxes across gradients of land use and water table. I don’t see this reflected in the set up: if we forget about the slope site (only two measurement days), you only have two systems, so we can hardly call this a gradient. It is completely unclear how comparable they are in there topographic setting: is the disturbed field like the forest site, but then converted? Is the water table at the same level in both? Furthermore: how don’t really identify the environmental drivers at play, right? You just measured all of them, but did not really quantify the importance of one vs. the others in governing the GHG balance? It’s more that you look at some bivariate correlations and explain those, rather than to work with the full set of explanatories you have at hand.
- I’m in general not against having a joint ‘results and discussion’ section, but in this case it becomes all very unclear. One (out of many) examples: in L154 you write ‘that nutrients may have enhanced heterotrophic CO2 and N2O production’, while at this point you did not report anything about the fluxes themselves yet.
- The language needs to improve, see some specific examples below.
Methodological unclarities:
- You installed the collars: but it is unclear whether these were installed once, and then re-used throughout the monitoring period? Or re-installed every time? Did you allow the collar to ‘equilibrate’ for a couple of days after installation? It has been shown that right after installation you disturb the soil enough to boost mineralization..
- For your He-O2 method: ig will be important here what you use for soil moisture levels in the incubation. You state the ‘flushing depended on the soil moisture’, but I don’t see how you set the moisture level? Did you just take the moisture from the soil as it was sampled? How long between the sampling and the incubation (also important for N depletion etc.).
- Did you overpressurize when transferring the gas samples from the chambers to the 50ml glass vials? Not doing so will likely introduce dilution effects when transferring the sample to the GC…
- How did you ‘observe’ water table height in the observation wells? Just visually?
- L 115: a peat sample was collected from each chamber after the sampling sessions in September and March à do you mean after each session? Does this mean that you reinstalled chambers at every sampling occasion? Cfr. Comment above: then your fluxes would likely be affected by the disturbance of forcing a chamber collar in the soil.
- Slope monitoring: so 4 ‘sampling’ events, clustered on two consecutive days. So basically two days of monitoring. Same day measurements are obviously not independent and temporally autocorrelated (you also need the statistical tools to deal with that in your correlations, correlation and GAM assume independent samples). I’m sorry, but that is really too limited to go to a GHG balance. More general: the monitoring took place on a different amount of days in the three sites, and on different time points. This would be “ok-ish” to go to inter-site comparisons if you would have a lot of measurements, but with the limited sample set, I don’t see how you can scientifically justify these comparisons. Especially not if your manuscript conclusion is ‘Our study shows that even moderate drying in the Peruvian palm swamps may create a devastating feedback on climate change through CO2 and N2O emissions.”. That’s just a dramatic overstating of your data. It’s not even clear what you mean by that: do you mean the agricultural vs. forest site comparison? I guess not, since the N2O and CO2 fluxes are in the same range there? So it must be that you mean the drying of the forest site itself? But I do not see data to support that statement? All unclear to me, after having spent quite some time with this manuscript, and that is not how it’s supposed to be unfortunately.
Some specific comments, but not exhaustive I’m afraid:
- Title: ‘High’ relative to what??
- L19: ‘remove’ large amounts of CO2 -> you make it sound as if the flux into the system is exceptionally high, while it’s my understanding that it’s mainly the stock that is high. So ‘store’ would be better here.
- L27: retaining their high CH4 -> rephrase
- L38: undisturbed peat swamp forests sequester carbon for tens of kyr. Do you mean: have been sequestering carbon for the past millennia?
- L52: unclear: the amazon has an exceptionally high 10% share of nitrification in N2O production. Do you mean that 10% of the produced NO3 is further emitted through N2O?
- L60: a quickly increasing disturbance à not proper English.
- L62: where is your reference for ‘droughts increase ecosystem respiration’? Kind of a general statement as well, no?
- L63: explain what you mean with that positive feedback loop for the reader, please.
- L106: how many datapoints did you set to 0?
- L106: you should add a statement on why you would use a linear, and not a quadratic, fit.
- L165: ‘the dry station’ à do you mean the slope? Not clear: be consistent in your naming of your sites.
- L167: that station represents the optimal soil moisture: you cannot say this. You make a relative comparison here, while optimal would be on an ‘absolute’ basis.
- Figure 6: do you really need to show the P-value until 8 numbers after the decimal?
- L208: when you make a comparative statement like this, it would be good to also give those numbers to the reader. ‘Agreed with huge N2O emissions from floodplains’ à how high where those ‘huge’ fluxes.
- L230: consistently use N2O-N please.
- L213-227 is a long speculation of several potential reasons for the combined observation of low NO3 and low N2O. At line 224 the authors write ‘third’, while this is already the fourth potential reason. This whole section is speculative and can be shortened in my opinion.
- L235: where is the toe-slope?
- L233:manioc field: be consistent in the naming
- L260-261: very strange sentence at this spot.
- L 263: please be consistent in the naming of your different systems. What do you mean with arable peatland? The agricultural fields? Use this throughout the manuscript.
- L266-267: high nitrifier denitrification while suppressing the full denitrification pathway à strange formulation: you show high N2 outgassing in your earlier section?
- Also: you actually don’t show nitrifier denitrification. You list a number of potential mechanisms and many rely on earlier work to say that it is ‘likely’ nitrifier denitrification. You would need tracing or isotopocule data to infer that.
Citation: https://doi.org/10.5194/bg-2021-46-RC2 -
AC2: 'Reply on RC2', Jaan Pärn, 11 Jul 2021
I have now reviewed ‘High greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon’ by Pärn et al.
This study discusses results from monitoring GHG in peatlands under various land-use systems, in the Peruvian Amazon. The issue that is raised in the paper is important and timely. Anthropogenic pressure is increasingly threatening natural peatland systems, with potential important outcomes for the regional C and GHG balance.
Thank you for the thorough review and recognition of importance.
However, I’m left a bit disappointed after having read the paper. There are too many issues and unclarities to recommend this paper for publication. And I must say that I have not enough information to assess the scientific validity of the version (see the major issues below). In my opinion, this paper needs to be rewritten to be acceptable anywhere. I have tried to give a list of ‘constructive’ comments below, which might help in this process.
Thank you for the comments, we will rewrite the MS accordingly.
Important, and a bit less constructive I’m afraid, is that the dataset will remain limited. To me, it seems more like an exploratory dataset that could go in a proposal for more detailed work on this, or for a kind of perspectives piece somewhere, rather than a full research article. You cannot really go to comparing the anthropogenic impact on full GHG balances with only two systems
We acknowledge the limits and the exploratory nature of our dataset. We have not claimed However, we feel that the near-simultaneous comparisons of sites under various land uses, and the hot moment of N2O emission in our observations are important and timely enough to be published in an interactive open-access journal like Biogeosciences. We will certainly tone down the generality of conclusions and try to keep within the limits of our observations.
(I don’t consider the slope site as included, only two days of measurements – we have to draw the line somewhere…)
We agree that the Slope site includes the same number of observations as a subset of the other sites, and thus does not carry the same weight as the other sites. We do not rely on any time-series analysis of the Slope site. We already excluded the Slope site from a number of analyses, such as the one presented in Figure 6. However, as the PC plot (Figure 3) shows, the Slope site sits between the Swamp and Manioc sites as expected. Within the site, soil respiration follows the water table depth, as expected. Thus, it is fair to say that despite the low number of measurements and a lack of a dimension of time, the site, rather than creating erratic noise, complements the land use gradient from a pristine swamp to an intensively used agricultural field.
with minimal data (a handful of measurements
We agree that the data are insufficient for annual GHG budgets, and we will remove all statements implying those.
during half of a hydrological year, mainly confined in one season?).
We did not time our study period to any season, nor can it be confined in a single season. The start of our study period in September 2019 is most accurately described as the end of the dry season. However, the ensuing rains only lasted up until late December. The area received hardly any rain from January till March. We do agree that an annual upscaling of GHG fluxes from this rather atypical weather is a stretch. We will remove the results of the upscaling.
You also cannot really go to mechanisms, since the in-depth work is missing a bit…
Indeed, we cannot exclusively identify nitrifier denitrification as the mechanism of N2O production. Therefore, we agree to remove the statement from the Abstract and Conclusions. However, the absence of nitrate still rules out denitrification and nitrification leaving nitrifier denitrification as the only candidate mechanism that directly produces N2O in the soil. Moreover, as Hergoualc’h et al. (2020) identified nitrifier denitrification as the main N2O production mechanism in the site before, we feel that the discussion in lines 211–226 is justified.
The study sites are not well enough described for an informed reader to understand:
We will be happy to elaborate the study site description.
- I work on GHG balances of tropical ecosystems, but not specifically in peatland complexes. However, I did not understand the seasonality (or lack thereof) of inundation
As explained above, it would be confusing to explain seasonality in this study period. The start of our study period in September 2019 is most accurately described as the end of the dry season. The ensuing rains raised the water table to the ground level but only lasted up until late December. The area received hardly any rain from January till March, during which the water table remained close to the ground level. We will include the water table dynamic in the site description.
how the disturbed systems were drained (or not) before they were planted with agricultural crops. This really impedes the understanding of this paper, even for readers with interest and expertise in this topic.
The Slope and Manioc sites were not ditch-drained. The main factors that effected their drying were their location on slopes, the slash and burn of forest and conventional hand-hoe tillage. We will provide information on the land-use history in the site description.
For me as a reviewer: you measured only from September to March (approx.. half a year) – it is unclear whether this encompasses a certain season
The start of our study period in September 2019 is most accurately described as the end of the dry season. The ensuing rains raised the water table to the ground level but only lasted up until late December. The area received hardly any rain from January till March, during which the water table remained close to the ground level. We will include the water table dynamic in the site description.
whether your upscaling to a year makes sense.
The idea of the upscaling was to put our numbers into the context of the extent of peatland area potentially under threat. Indeed, the study period did not cover typical seasonality, but it did involve broadly the same alteration between showers and dryness as a normal year in the area. As a bottom line, we propose to remove the results of the upscaling from the manuscript and find other ways to provide context for the results.
I actually looked up the seasonality myself: you monitored the rainy season if I’m correct?
September to March would be a rainy season in a normal year, but hardly any rain fell from January till March. Therefore, it would be misleading to call it a typical rainy season for the Peruvian Amazon.
Than why not the dry season as well? And how would that affect your conclusions??
We did not design our study to represent a typical or any year. A main assumption of our study was that the GHG result from the immediate environmental conditions. Thus, apart from issues with the upscaling, our conclusions remain valid.
- Additionally, you write in L 85: “on the slope and manioc sites, we installed three toposequent stations … “. Some more info is needed here: what was the exact setup.
We will provide landscape profiles to the study site description section.
And moreover: what with the forest sites? No toposequent stations? So how was the setup there, then?
The Swamp site was located in perfectly flat terrain. We established the chambers in no particular sequence to any topographic features. We will declare that in the site description.
Other major issues
The build-up and communication of the key message of the manuscript is problematic. The introduction actually shows this well: 1) Peatlands are important C stocks, 2) tropical peatlands vulnerable, 3) tropical peatlands are vulnerable, 4) very important for N2O, 5) diving into the mechanistics behind the N2O, 6) Amazon basin important for N2O globally, 7) again mechanistics in peatland N2O, then ending the paragraph with ‘Brazil is also a major contributor to the global increase in N2O emissions during the last decades, owing to the increase in N fertilization’. Then the next paragraph you continue suddenly on the C sequestration in the peat GHG balance. You go on about microbial C respiration and conclude than that drought-induced tree mortality is saturating the Amazon C sink. The tree dieback described in Hubau et al. (earlier shown by Brienen et al. in 2015) has nothing to do with a positive feedback loop of microbes that acclimatize to rising temperature. Also the link with this ‘drying’ of forests themselves through el nino effects and then your ‘human disturbance’ is not clear to me. Do you want to look at climate change effects on the peatland forests, or do you want to focus on the effects of converting forests to agricultural fields? Not clear. While many of the statements might be factually correct, it doesn’t necessarily set out a comprehensible intro for the reader.
Thank you for pointing out the inconsistencies in the text! We will order the statements more logically and remove the ones not directly relevant to the main points of the paper.
- Your end of your intro sets out the objectives: to fill the knowledge gap and to identify environmental drivers of GHG fluxes across gradients of land use and water table. I don’t see this reflected in the set up: if we forget about the slope site (only two measurement days), you only have two systems, so we can hardly call this a gradient. It is completely unclear how comparable they are in there topographic setting: is the disturbed field like the forest site, but then converted?
Generally – yes, both are on a peaty soil and practically every aspect of ecological difference between the two sites is caused by the slashing of forest, burning and agricultural use. We will describe the land use history in the study site section.
Is the water table at the same level in both?
As the extremely different soil water contents (0.8 m3 m–3 vs 0.15 m3 m–3) indicate, the water table was close to the ground in the Swamp site while it was about 1.5m below the ground in the Manioc site. Before the slash-and-burn agriculture, the water table was, on average, at the same level
Furthermore: how don’t really identify the environmental drivers at play, right? You just measured all of them, but did not really quantify the importance of one vs. the others in governing the GHG balance? It’s more that you look at some bivariate correlations and explain those, rather than to work with the full set of explanatories you have at hand.
We did test the correlations between the greenhouse gas fluxes and all environmental characteristics, both within and across the sites. We only displayed the significant correlations and, to tighten the communication, we did not display the insignificant correlations. However, to quantify the relative importance of the significant correlations, it is probably best to show the correlation matrices.
- I’m in general not against having a joint ‘results and discussion’ section, but in this case it becomes all very unclear. One (out of many) examples: in L154 you write ‘that nutrients may have enhanced heterotrophic CO2 and N2O production’, while at this point you did not report anything about the fluxes themselves yet.
We agree to move the discussion to a separate section.
- The language needs to improve, see some specific examples below.
We will ask a native English-speaking editor to proofread the manuscript.
Methodological unclarities:
- You installed the collars: but it is unclear whether these were installed once, and then re-used throughout the monitoring period? Or re-installed every time? Did you allow the collar to ‘equilibrate’ for a couple of days after installation? It has been shown that right after installation you disturb the soil enough to boost mineralization..
We installed the collars twice: early September and early January, and allowed a stabilisation time of several days before the sampling. We will specify this in the Methods section.
- For your He-O2 method: ig will be important here what you use for soil moisture levels in the incubation. You state the ‘flushing depended on the soil moisture’, but I don’t see how you set the moisture level? Did you just take the moisture from the soil as it was sampled?
Our statement ’The flushing time depended on the soil moisture.’ is just an a posteriori observation on how long it took to establish the new equilibrium in the intact soil core, i.e. to replace the air inside (mostly containing N2) with the artificial gas mixture. Therefore, we did not set the moisture level, we just replaced the soil air and report that the flushing time was longer in the wetter soils.
How long between the sampling and the incubation (also important for N depletion etc.).
Transport and storage time after the sampling was approximately a week.
- Did you overpressurize when transferring the gas samples from the chambers to the 50ml glass vials? Not doing so will likely introduce dilution effects when transferring the sample to the GC…
We did not overpressurise but our GC system does is fully sealed and under vacuum, thus excluding any dilution with lab air. The GC demand of gas is 25–30ml, which is half the volume of our 50ml sample. The vacuum pulls the gas sample into the sealed system.
- How did you ‘observe’ water table height in the observation wells? Just visually?
We observed water table height using a tape measure. We will specify this in the Material and Methods section.
- L 115: a peat sample was collected from each chamber after the sampling sessions in September and March à do you mean after each session? Does this mean that you reinstalled chambers at every sampling occasion? Cfr. Comment above: then your fluxes would likely be affected by the disturbance of forcing a chamber collar in the soil.
As we state in the Material and Methods section, we collected soil twice: “A peat sample of 150 to 200 g was collected from each chamber between 0 to 0.1 m depth after the sampling sessions in September and March.” We installed the collars twice: early September and early January, and allowed a stabilisation time of several days before the gas sampling. We will specify this in the Material and Methods section.
- Slope monitoring: so 4 ‘sampling’ events, clustered on two consecutive days. So basically two days of monitoring. Same day measurements are obviously not independent and temporally autocorrelated (you also need the statistical tools to deal with that in your correlations, correlation and GAM assume independent samples). I’m sorry, but that is really too limited to go to a GHG balance. More general: the monitoring took place on a different amount of days in the three sites, and on different time points. This would be “ok-ish” to go to inter-site comparisons if you would have a lot of measurements, but with the limited sample set, I don’t see how you can scientifically justify these comparisons.
Thank you for the critical evaluation of our Slope sample. Not sure, though, whether the gas samples from the same site on different months are statistically independent from each other and whether that is an essential problem. We acknowledge that the monitoring of the Slope site was short, and the data can only be used to compare with subsamples of similar extent, such as the September observations of the Swamp and Manioc sites (like in Fig. 7).
- Especially not if your manuscript conclusion is ‘Our study shows that even moderate drying in the Peruvian palm swamps may create a devastating feedback on climate change through CO2 and N2O emissions.”. That’s just a dramatic overstating of your data.
We agree that this statement tried to summarise too many results into one general statement. We will remove this statement and add sentences that are more directly limited with our results.
- It’s not even clear what you mean by that: do you mean the agricultural vs. forest site comparison? I guess not, since the N2O and CO2 fluxes are in the same range there? So it must be that you mean the drying of the forest site itself? But I do not see data to support that statement? All unclear to me, after having spent quite some time with this manuscript, and that is not how it’s supposed to be unfortunately.
This statement encompassed two observations: 1) The Manioc field retained high CO2 and N2O emissions after the conversion (which itself caused high but unmeasured CO2 emissions from burning, and prevented CO2 sequestration in trees); 2) We link the high CO2 and N2O emissions from the Swamp forest with the seasonal water table drawdown. We agree that the points can be communicated better and will try to break them down better.
Some specific comments, but not exhaustive I’m afraid:
- Title: ‘High’ relative to what??
Substantial comment. What we meant is high relative to sequestration or zero balance. However, probably it is better to remove this adjective from the title.
- L19: ‘remove’ large amounts of CO2 -> you make it sound as if the flux into the system is exceptionally high, while it’s my understanding that it’s mainly the stock that is high. So ‘store’ would be better here.
Agreed.
- L27: retaining their high CH4 -> rephrase
Agreed.
- L38: undisturbed peat swamp forests sequester carbon for tens of kyr. Do you mean: have been sequestering carbon for the past millennia?
We mean thousands of years but the policy of Biogeosciences is not to use words for numbers but to use k for thousands. However, if that is misleading, we will be glad to use millennia instead.
- L52: unclear: the amazon has an exceptionally high 10% share of nitrification in N2O production. Do you mean that 10% of the produced NO3 is further emitted through N2O?
The ‘high 10% share of nitrification in N2O production’ means 10% of the N2O is produced in nitrification. Denitrification and other processes are responsible for the 90%. However, it may be that this point is too specific for the introduction.
- L60: a quickly increasing disturbance à not proper English.
We will let a native-speaking editor to proofread the manuscript.
- L62: where is your reference for ‘droughts increase ecosystem respiration’? Kind of a general statement as well, no?
For us, the fact that soil drying and warming increase ecosystem respiration is textbook material. We will cite a reference for that.
- L63: explain what you mean with that positive feedback loop for the reader, please.
Agreed.
- L106: how many datapoints did you set to 0
We set 32 out of the 165 N2O datapoints to 0. We did not set any CO2 or CH4 datapoints to 0. We will include the information in the Material and Methods section.
- L106: you should add a statement on why you would use a linear, and not a quadratic, fit.
Agreed. The linear fit is the only one that does not assume either saturation or quasi-exponential rise in concentration.
- L165: ‘the dry station’ à do you mean the slope? Not clear: be consistent in your naming of your sites.
‘The dry station (water table –0.7 m; soil water content 0.26 m3 m–3; soil temperature around 26 ºC at 10 cm depth) of the young swamp forest’ is the dry station of the Slope site. We will correct that.
- L167: that station represents the optimal soil moisture: you cannot say this. You make a relative comparison here, while optimal would be on an ‘absolute’ basis.
The point here is that we observed the highest soil respiration at this moisture, not the driest one.
- Figure 6: do you really need to show the P-value until 8 numbers after the decimal?
We can just state ‘p<0.01’ but not sure whether that would convey the same information.
- L208: when you make a comparative statement like this, it would be good to also give those numbers to the reader. ‘Agreed with huge N2O emissions from floodplains’ à how high where those ‘huge’ fluxes.
We will provide the figures from the earlier papers.
- L230: consistently use N2O-N please.
Will do that.
- L213-227 is a long speculation of several potential reasons for the combined observation of low NO3 and low N2O. At line 224 the authors write ‘third’, while this is already the fourth potential reason. This whole section is speculative and can be shortened in my opinion.
Agreed. We will shorten that paragraph.
- L235: where is the toe-slope?
We will specify that.
- L233:manioc field: be consistent in the naming
Agreed.
- L260-261: very strange sentence at this spot.
We will remove it.
- L 263: please be consistent in the naming of your different systems. What do you mean with arable peatland? The agricultural fields? Use this throughout the manuscript.
Agreed.
- L266-267: high nitrifier denitrification while suppressing the full denitrification pathway à strange formulation: you show high N2 outgassing in your earlier section?
N2O is the intermediate product of denitrification. High N2O emission with high denitrification potential itself is evidence of incomplete denitrification. The N2 potential in the Swamp measurements was high in September compared to the other, dry sites but it was modest compared to the long-inundated March samples with low N2O emissions.
- Also: you actually don’t show nitrifier denitrification. You list a number of potential mechanisms and many rely on earlier work to say that it is ‘likely’ nitrifier denitrification. You would need tracing or isotopocule data to infer that.
A fair point. We agree to remove the statement from the Abstract and Conclusions and shorten the discussion in lines 211–226. However, the absence of nitrate still rules out denitrification and nitrification leaving nitrifier denitrification as the only candidate mechanism that directly produces N2O in the soil. In addition, Hergoualc’h et al. (2020) identified nitrifier denitrification as the main N2O production mechanism in the site. Therefore, we will keep nitrifier denitrification in the discussion in lines 211–226.
Citation: https://doi.org/10.5194/bg-2021-46-AC2
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RC3: 'Comment on bg-2021-46', Anonymous Referee #3, 03 Aug 2021
PaÌrn et al., 2021 report greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon. The investigated peatland sites covered (1) a slash-and-burn manioc field, (2) a 12-year-old secondary forest grown over a fallow pasture and a banana plantation, and (3) a natural swamp forest. While I very much acknowledge the scientific effort of data collection from a strongly understudied region of the world, I am afraid that the manuscript suffers in its current form from insufficient structural and scientific quality. This is a pity, since the additional laboratory analyses to quantify N2 potential from soil cores from the studied sites are novel and interesting.
Generally, the introduction is weak and does not clearly introduce why studying greenhouse gases from peatlands under various disturbances is important. The introduction mentions nowhere methane which is probably the most important greenhouse gas in these ecosystems and only a couple of lines are spent on carbon dioxide. Moreover, the data coverage is poor; Only 9 sampling sessions, over a period of 7 months (Sept 2019 to March 2020) were conducted at two sites (swamp forest; manioc field) and only four sessions during two consecutive days in Sept 2020 were conducted at the remaining secondary forest site. The reader is left with no explanation on why this irregular sampling strategy was chosen. Lastly, the discussion section does not contextualize the findings with other scientific literature, especially the aspect of disturbance. The word disturbance does not even appear in the discussion. Again, methane as an important greenhouse gas in these ecosystems is barely discussed. Given these substantial drawbacks of the study I recommend rejection of the paper in its current form.
Specific comments:
Abstract
General: The Abstract suffers from vague statements and needs to be more concise.
Line 22: Which ‘changes’? Land-use? Climate?
Line 25: At which frequency?
Line 26: moderate compared to? Give concrete flux numbers.
Line 27: ‘slight water table drawdown’. Pls be more specific. From inundated conditions? How much is ‘slight’
Line 29: ‘Nitrifier-denitrification was the likely source mechanism’ based on which underlying data? This is too speculative.
Introduction:
Line 42-45: How do these numbers relate to each other? Does that mean that these peatlands are a hotspot within the Amazon rainforest hotspot?
Line 54: This sentence is out of context.
Line 59: There is no transition to the C cycle and related CO2 emissions.
Line 62: Can you give a reference for this statement. Drought first and foremost reduces photosynthesis and consequently less assimilates are available for autotrophic and heterotrophic respiration.
Line 65: consider a better transition to the soil part of the intoduction
Materials and Methods:
General: No structuring into subsections
Line 76: suggest renaming site to ‘Swamp primary forest’
Line 76: suggest renaming site to ‘Swamp secondary forest’
Figure 2: what is the Pastaza-MaranÌon Basin? This should be mentioned in the text as well.
Line 85: How many chambers were installed at the swamp site?
Line 85: stations? Why not calling them plots?
Line 86: How long before gas sampling where the collars installed?
Line 92: How much gas was sampled and how? With a syringe and needle through a septum?
Line 100: How was CO2 measured? How was the GC calibrated?
Line 104: How much of the data was affected by this quality check?
Line 128: A ~7cm by 6cm soil core is not very representative.
Line 137: How were the samples taken from the continuously flushed vessel?
Line 137: How was this done exactly? N2 is not easy to measure. How was the GC calibrated?
Line 138: Give equation.
Results and Discussion
Line 154-159: Can the water table change be illustrated graphically along with the actual fluxes of CO2, CH4, and N2O?
Line 155: ‘slope forest’ is not the same site name as specified in the methods. Same for ‘palm swamp’.
Line 165: dry station? I assume the authors refer to the toposequent stations? This needs to be clarified in the method section. Line 166: which site is the ‘young swamp forest’?
Line 167: Why does the dry station represent the optimal moisture for soil respiration?
Line 172: Which site is the swamp peat?
Figure 4: Not been referred to in the text. I guess this should be done in line 173.
Figure 5: Why not CO2 flux instead of soil respiration. That would be more in line with the other fluxes.
Line 176: I assume the authors refer to the eddy covariance technique.
Line 180: prevail --> dominate
Line 188-194: 6 lines of discussion for CH4 only. This needs to be extended.
Line 195-198: Sudden switch to N2O fluxes with mentioning of soil respiration. Hard to follow the discussion.
Line 200: From what do the authors conclude at this point that N2O was produced from NH4?
Line 211-227: Very speculative paragraph.
Line 235: toe-slope swamp forest? Same as site ‘slope’?
Line 238: Are there any other papers which investigate N2O reduction to N2 in tropical systems? What are the implications for the N cycle?
L251: Upscaling paragraph lacks info on CH4.
Citation: https://doi.org/10.5194/bg-2021-46-RC3 -
AC3: 'Reply on RC3', Jaan Pärn, 23 Aug 2021
Pärn et al., 2021 report greenhouse gas fluxes from peatlands under various disturbances in the Peruvian Amazon. The investigated peatland sites covered (1) a slash-and-burn manioc field, (2) a 12-year-old secondary forest grown over a fallow pasture and a banana plantation, and (3) a natural swamp forest. While I very much acknowledge the scientific effort of data collection from a strongly understudied region of the world, I am afraid that the manuscript suffers in its current form from insufficient structural and scientific quality. This is a pity, since the additional laboratory analyses to quantify N2 potential from soil cores from the studied sites are novel and interesting.
Generally, the introduction is weak and does not clearly introduce why studying greenhouse gases from peatlands under various disturbances is important. The introduction mentions nowhere methane which is probably the most important greenhouse gas in these ecosystems and only a couple of lines are spent on carbon dioxide. Moreover, the data coverage is poor; Only 9 sampling sessions, over a period of 7 months (Sept 2019 to March 2020) were conducted at two sites (swamp forest; manioc field) and only four sessions during two consecutive days in Sept 2020 were conducted at the remaining secondary forest site. The reader is left with no explanation on why this irregular sampling strategy was chosen. Lastly, the discussion section does not contextualize the findings with other scientific literature, especially the aspect of disturbance. The word disturbance does not even appear in the discussion. Again, methane as an important greenhouse gas in these ecosystems is barely discussed. Given these substantial drawbacks of the study I recommend rejection of the paper in its current form.
Thank you for the thorough and fair comment. We will take the points forward and improve the manuscript accordingly. Indeed, we took the importance of GHG from various disturbances in the tropics for granted to the reader of the journal. We tried to keep the introduction brief and summary at the expense of widely known detail on methane and carbon dioxide fluxes. We also spared the reader from technical details on sampling strategy planning. We also agree on the reviewer’s criticism on the underuse of the general concept of disturbance. We believe the manuscript will substantially benefit from expansion on these points and will be glad to improve on them.
Specific comments:
Abstract
General: The Abstract suffers from vague statements and needs to be more concise.
Agreed. We will remove all statements that are vaguely connected to the main discussion.
Line 22: Which ‘changes’? Land-use? Climate?
The statement referred to the changes mentioned in the couple of statements above – drought, cultivation and other changes contributing towards the varying oxygen content. However, we will remove this vague statement.
Line 25: At which frequency?
We will detail the frequency here.
Line 26: moderate compared to? Give concrete flux numbers.
Agreed. We will provide the information.
Line 27: ‘slight water table drawdown’. Pls be more specific. From inundated conditions? How much is ‘slight’.
Good point. We will provide the change in water table in cm from the inundated level.
Line 29: ‘Nitrifier-denitrification was the likely source mechanism’ based on which underlying data? This is too speculative.
Indeed, we cannot exclusively identify nitrifier denitrification as the mechanism of N2O production. Therefore, we agree to remove the statement from the Abstract and Conclusions. However, the absence of nitrate still rules out denitrification and nitrification leaving nitrifier denitrification as the only candidate mechanism that directly produces N2O in the soil. Moreover, as Hergoualc’h et al. (2020) identified nitrifier denitrification as the main N2O production mechanism in the site before, we feel that the discussion in lines 211–226 is justified.
Introduction:
Line 42-45: How do these numbers relate to each other? Does that mean that these peatlands are a hotspot within the Amazon rainforest hotspot?
Yes, the Peruvian peatlands are a potential contributor within the larger Amazonian hotspot, and we will alter the sentence to state that.
Line 54: This sentence is out of context.
True. The statement needs a transition sentence.
Line 59: There is no transition to the C cycle and related CO2 emissions.
We intended this paragraph as a summary of all three GHGs. However, we take the point that in this form it may be misleading to the C fluxes again. We will restructure the Introduction section for a more logical order.
Line 62: Can you give a reference for this statement. Drought first and foremost reduces photosynthesis and consequently less assimilates are available for autotrophic and heterotrophic respiration.
A FLUXNET synthesis (Schwalm et al. 2010 Global Change Biology) should do the job.
Line 65: consider a better transition to the soil part of the introduction
Agreed.
Materials and Methods:
General: No structuring into subsections
Indeed, we did not structure this section into subsections like we did not anywhere else. However, we will consider the structuring here.
Line 76: suggest renaming site to ‘Swamp primary forest’
Line 76: suggest renaming site to ‘Swamp secondary forest’
The correct order of words would probably be ‘Primary swamp forest’ and ‘Secondary swamp forest’. Otherwise, we agree.
Figure 2: what is the Pastaza-MaranÌon Basin? This should be mentioned in the text as well.
Agreed. We will define the basin in the text.
Line 85: How many chambers were installed at the swamp site?
The number is 10. We will state that in the text.
Line 85: stations? Why not calling them plots?
The even more correct name is ‘point’. We will change that throughout the text.
Line 86: How long before gas sampling where the collars installed?
We allowed a stabilisation time of several days before the sampling. We will specify this in the Methods section.
Line 92: How much gas was sampled and how? With a syringe and needle through a septum?
We sampled the gas through tubes and medical three-way taps straight into 50mL vials. We will specify this in the Methods section.
Line 100: How was CO2 measured? How was the GC calibrated?
We determined CO2 concentration with the same flame ionisation detector. We will specify the calibration in the text.
Line 104: How much of the data was affected by this quality check?
We set 32 out of the 165 N2O datapoints to 0. We did not set any CO2 or CH4 datapoints to 0. We will include the information in the Material and Methods section.
Line 128: A ~7cm by 6cm soil core is not very representative.
It is representative of the 50cm diameter collar. We sampled a soil core from each collar.
Line 137: How were the samples taken from the continuously flushed vessel?
Through a tube reaching the headspace through a hermetic septum.
Line 137: How was this done exactly? N2 is not easy to measure. How was the GC calibrated?
We detected N2 concentration on the same analyser as N2O. N2 concentration is not more difficult to measure than N2O (at least we have not seen it stated in literature as such). N2 flux is difficult to measure, but we solved this with the intact soil core technique. We will provide detail on the N2 concentration detection and its calibration.
Line 138: Give equation.
Will do that.
Results and Discussion
Line 154-159: Can the water table change be illustrated graphically along with the actual fluxes of CO2, CH4, and N2O?
Yes, we will do that.
Line 155: ‘slope forest’ is not the same site name as specified in the methods. Same for ‘palm swamp’.
We will change the text for consistency in the site names.
Line 165: dry station? I assume the authors refer to the toposequent stations? This needs to be clarified in the method section.
We will name the toposequent transect points in the Methods section.
Line 166: which site is the ‘young swamp forest’?
This is the Slope site. We will change the statement consistency in the site names.
Line 167: Why does the dry station represent the optimal moisture for soil respiration?
Both dryness and wetness (lack of soil oxygen) may curb soil respiration. The dry point had intermediate soil moisture and showed the highest respiration rates.
Line 172: Which site is the swamp peat?
It is “The Swamp peat …”. We defined the sites in lines 76–78. According to that, the Swamp was “a natural forest in the Quistococha lake floodplain”.
Figure 4: Not been referred to in the text. I guess this should be done in line 173.
We will correct that.
Figure 5: Why not CO2 flux instead of soil respiration. That would be more in line with the other fluxes.
‘CO2 flux’ would be wrong as our opaque chambers exclude photosynthesis and only represent soil respiration.
Line 176: I assume the authors refer to the eddy covariance technique.
Yes, will specify that.
Line 180: prevail --> dominate
We will change that.
Line 188-194: 6 lines of discussion for CH4 only. This needs to be extended.
We will do that.
Line 195-198: Sudden switch to N2O fluxes with mentioning of soil respiration. Hard to follow the discussion.
The switch follows a paragraph break, so it is hardly more sudden than the switch from CO2 to CH4. However, we should probably emphasise the paragraph break more. The surge in soil respiration caused by the water-table drawdown should probably be introduced in the CO2 paragraph.
Line 200: From what do the authors conclude at this point that N2O was produced from NH4?
We stated in line 149: “The waterlogged swamp peat did not contain a detectable amount of NO3–.” This leaves only NH4 and its non-NO3 products as potential sources of N2O.
Line 211-227: Very speculative paragraph.
Not sure what would be a more adequate discussion of the N2O fluxes, soil NH4, NO3, water and O2 content measurements and candidate mechanisms behind the N2O fluxes listed in the literature, including earlier corroborating studies at the same site.
Line 235: toe-slope swamp forest? Same as site ‘slope’?
Yes. We will standardise the site naming throughout the text.
Line 238: Are there any other papers which investigate N2O reduction to N2 in tropical systems? What are the implications for the N cycle?
No, to our knowledge not. We state the main implication for the N cycle in line 241: “Thus, the N2O likely produced from nitrifier denitrification in March was consumed by denitrification.”
L251: Upscaling paragraph lacks info on CH4.
Following the suggestions of the other two reviewers, we will remove the upscaling paragraph altogether.
Citation: https://doi.org/10.5194/bg-2021-46-AC3
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AC3: 'Reply on RC3', Jaan Pärn, 23 Aug 2021
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