the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 24 Jun 2026
Groundwater-Level Response of Annual CO2 Budgets from a Dutch Eddy Covariance Network: Comparison with European Temperate Peatlands across Land Use and Sites
Abstract. Peatlands in the Netherlands hold significant cultural, agricultural, and ecological value but also contribute substantially to national greenhouse gas (GHG) emissions as a result of drainage. This necessitates urgent mitigation, leading to the implementation of various land and water management strategies. As part of the Dutch national GHG research program (NOBV), eddy covariance (EC) measurements of carbon dioxide (CO2) fluxes were conducted at 20 sites, encompassing managed peat meadows, wet nature areas, and paludiculture systems over periods of 1 to 3 years. A novel mobile EC set-up was utilized at some locations to enhance spatial coverage.
Net Ecosystem Exchange (NEE) of CO2 demonstrated pronounced seasonal dynamics across different land-use types. Wet and highly productive systems exhibited both elevated uptake and emissions, leading to intervals of net CO2 uptake. Managed pastures were typically net emitters on a daily timescale, except during early summer when assimilation peaked. Although annual net ecosystem carbon balance (NECB) estimates were subject to uncertainty due to data gaps and adjustments for harvest, grazing, and manure application, systematic differences between land-use types remained evident. To assess the sensitivity of CO2 emissions to groundwater dynamics, ecological response functions (ERFs) were employed to relate NECB to groundwater depth, and these relationships were compared with findings from the literature. Across all sites, NECB exhibited only a weak association with mean annual groundwater level when referenced to the soil surface (ERF slope approximately 0.5 t CO2 ha-1 yr-1 cm-1, R2 = -0.08), and an even weaker association with mean summer groundwater level. When groundwater depth was referenced to the clay layer, the inferred ERF sensitivity increased, resulting in steeper slopes of about 0.8 t CO2 ha-1 yr-1 cm-1 (R2 = 0.26), although the overall explanatory power remained limited. These ERF-based sensitivities align with previously published ERFs, including studies that report non-linear groundwater–CO2 responses and threshold behavior.
Groundwater management interventions produced mixed effects on NECB. Of the pasture-oriented measures, only the Active Water Infiltration System (AWIS) resulted in a detectable shift in NECB beyond background interannual variability, while other interventions were not distinguishable from within-land-use variability. By contrast, clearer categorical patterns emerged across land-use and soil classes, and paludiculture systems showed lower net CO2 emissions than drained managed grasslands, and sites with a clay cap consistently emitted less CO2 than pure peat under comparable management. Overall, these results indicate that although mean groundwater metrics have limited predictive power at the site-year level, CO2 emissions at landscape scales are primarily governed by land use and the presence of a clay-layer, which defines the baseline against which water-management measures operate.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2026-3151', Anonymous Referee #1, 19 Aug 2026
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AC1: 'Comment on egusphere-2026-3151', Laurent Bataille, 19 Aug 2026
Erratum for one site - After submission, we noted that an incorrect data file had been used for the Ilperveld site. The analyses and results reported for this site will therefore change, and corrected results will be provided in the final version of the manuscript. Because this site represents only a very small fraction of the dataset, the general results and conclusions are not significantly impacted.
Citation: https://doi.org/10.5194/egusphere-2026-3151-AC1 -
RC2: 'Comment on egusphere-2026-3151', Inge Wiekenkamp, 06 Sep 2026
I have read the manuscript entitled “Groundwater-Level Response of Annual CO₂ Budgets from a Dutch Eddy Covariance Network: Comparison with European Temperate Peatlands across Land Use and Sites,” written by Laurent Bataille and coauthors and considered for publication in Biogeosciences. I think the topic is timely and highly relevant, and the manuscript presents an impressive dataset together with a substantial number of analyses. However, I also think that several aspects of the manuscript could be improved to strengthen its clarity, focus, and overall presentation. I have provided general and detailed comments below, together with suggestions for improvement.
General Comments:
1) Title: I think the title, “Groundwater-Level Response of Annual CO₂ Budgets from a Dutch Eddy Covariance Network: Comparison with European Temperate Peatlands across Land Use and Sites,” is quite lengthy, and it is not immediately clear what the article is about at first glance. I suggest shortening the title and making it more concise and intuitive, while still capturing the main focus of the study.
At present, the title seems to combine two different focal points: (1) the relationship between groundwater levels and CO₂ fluxes, and (2) the comparison of the Dutch data with data from temperate peatlands across Europe. Given that the manuscript focuses substantially on the relationship between groundwater levels and peatland CO₂ fluxes, the title could potentially be framed more explicitly around this central research question. A question-based or finding-based title could also help make the main objective and scientific motivation more apparent to the reader. At the same time, land use and management practices are also important themes throughout the manuscript. I therefore suggest that the authors consider which aspect (groundwater level, land use/management, or their interaction) is intended to be the primary focus of the paper and ensure that the title reflects this hierarchy.
2) Abstract: I think the general structure of the abstract is good. However, it may benefit from a stronger focus on the central research question and main take-home message. I found the key message of the ERF analysis somewhat difficult to discern, as several different findings are presented. First, the focus is on the relationship between carbon fluxes and groundwater level and the effect of adding information about the clay layer. Later, the focus shifts more towards land management. The statement that the ERF sensitivities “align with previously published ERFs” is not entirely clear to me, and it would be helpful to clarify what this comparison with previous studies demonstrates and how it relates to the main finding, so that the abstract is more self-contained.
More generally, I think the abstract would be strengthened by making the hierarchy of the results clearer, particularly the relative importance of groundwater level, land use, and the clay layer, and what these findings imply for groundwater-management strategies.3) Introduction: I like the content provided in the introduction, as it gives the reader the relevant background on peatlands and their CO₂ emissions. However, similar to the abstract, the introduction could benefit from a clearer focus. There is a substantial amount of knowledge and several relevant ideas presented, but I think the narrative would be stronger if the introduction more explicitly distinguished between (1) the current state of knowledge, (2) the specific knowledge gap, and (3) what new knowledge this study aims to provide.
4) Introduction – research questions: I think the research questions are well described, and the expected outcomes are also clearly presented. To make it easier for the reader to identify the overarching aim of the study, I suggest adding a sentence that brings the individual research questions together into a more general aim or purpose.5) Methodology: I think this section is generally clearly written. As a general suggestion, I would propose linking the methodological steps more explicitly to the overall aim of the study, so that the rationale for each analytical step is clearer throughout.
Regarding the machine-learning analysis, I feel that some methodological information is missing. First, how were the hyperparameters optimised, and which optimisation algorithm and objective function were used? Regarding the estimation of epistemic uncertainty, I also wonder why the authors chose 64 repeated model runs. Was the convergence or stability of the uncertainty estimate assessed? For example, does the estimated uncertainty stabilise after 20, 40, 64, or 100 runs? Without such an assessment or methodological justification, the choice of 64 runs is difficult to evaluate.
Additionally, the authors refer to the residual error as “aleatoric uncertainty”. Please clarify this terminology and discuss to what extent the residuals may also contain model misspecification, measurement error, and unresolved temporal or environmental variability. In other words, please clarify why the residual error is considered to represent predominantly irreducible variability rather than a combination of different sources of uncertainty.
For model performance evaluation, I would also expect one or more quantitative metrics, such as RMSE, MAE, and/or R², to be reported alongside the distributional and residual analyses. Looking only at the joint distributions and marginal densities may not sufficiently demonstrate how well the model reproduces the observed time series, particularly under specific conditions (e.g. day/night for sub-daily data, seasonal transitions, or extreme fluxes).
Finally, the use of LOOCV for model evaluation and uncertainty estimation may be problematic if individual observations are left out while temporally adjacent observations remain in the training set, given the strong temporal autocorrelation in flux data. Pointwise cross-validation may overestimate predictive performance under these circumstances, which could in turn lead to underestimated gap-filling uncertainty. I therefore suggest that the authors demonstrate that the reported model performance and uncertainty estimates are robust to temporally blocked validation, ideally using block lengths or gap structures that are representative of the actual missing-data periods.
6) Results: In the Results section, I suggest that the authors add a sentence at the beginning of each subsection explicitly linking the results to the aim of the study. This would help readers follow the overall narrative of the paper and more clearly understand why the particular results are being presented.
Also, several results are only shown in the Discussion section. I understand the intention, but if the authors intend to follow a classical Results and Discussion structure, I suggest that all results, including the corresponding figures and tables, are presented in the Results section rather than being introduced for the first time in the Discussion.
7) Water-level influence on carbon fluxes: While reading the manuscript, I was somewhat confused about the main message regarding the influence of groundwater level on carbon fluxes. In some parts of the Results, groundwater level is presented as a relatively weak predictor of annual NEE/NECB, with limited explanatory power (e.g. R² = −0.08 and R² = 0.26). In Section 3.6, however, the analysis of interannual changes in NECB and groundwater level shows a stronger relationship (R² = 0.37). Elsewhere in the manuscript, the authors describe groundwater level as showing clear and consistent relationships with carbon exchange. For example, the Conclusions state that “Groundwater level consistently emerged as a determinant of carbon exchange across sites and years.” I think the authors should clarify how these findings should be reconciled and ensure that the wording of the conclusions is consistent with the strength of the relationships demonstrated by the different analyses.
In particular, I suggest distinguishing more clearly between groundwater level being an important mechanistic or ecological driver of carbon exchange and groundwater level being a strong predictor of annual carbon balances in the present dataset. These are not necessarily equivalent: a variable can have a meaningful ecological effect or sensitivity while still explaining only a relatively modest proportion of the variation in annual NECB. If this is the interpretation intended by the authors, I suggest making this distinction explicit throughout the manuscript.
It would also be helpful to explain why changes in groundwater level appear to be more informative for explaining changes in NECB than mean groundwater level is for explaining annual NECB. Are these analyses intended to capture different aspects of the groundwater–carbon relationship? Making this distinction explicit would help the reader understand the apparently different strengths of the relationships reported throughout the manuscript.
Finally, regarding the comparison with previous literature, I think it would be useful to go beyond comparing the direction or slope of the reported relationships. Where possible, could the authors also compare the predictive or explanatory performance reported in previous studies and discuss why the groundwater–carbon relationship appears less pronounced in the present dataset? Differences in temporal or spatial scale, land management, vegetation, hydrological conditions, site selection, data processing, or the aggregation of fluxes into annual balances could potentially contribute to these differences.
8) Relationship to previous work and novelty: I think the manuscript needs to be more explicit about how it differs from, and advances beyond, previous work from the same research context. In particular, I see considerable conceptual overlap with the recent study on the groundwater–CO₂ relationship in Dutch peatlands (van der Poel et al., 2025), as well as some overlap with the study of methane emissions from Dutch peatlands (Buzacott et al., 2024).
Given the overlap in study region, measurements, authorship and, potentially, underlying datasets, I think the authors should provide a clear explanation of the specific scientific contribution of the present manuscript relative to these studies. In particular, it would be helpful to state explicitly what is novel in the present analysis—for example, in terms of research question, temporal or spatial scale, land-use comparison, analytical approach, variables considered, or interpretation of the groundwater–carbon relationship. This would also help clarify how the present study builds upon rather than duplicates previous work.Detailed Comments:
1) In line 33, the authors refer to the Dutch climate agreement policy document (“Klimaatakkoord”), which they cite as follows: Ministerie van Economische Zaken en Klimaat, 2019 - Ministerie van Economische Zaken en Klimaat: Klimaatakkoord, Government report, 2019. I suggest to adjust the citation to make it more complete and easier to find. I would add a link to the official document in English to make it easier to access and understand for the international audience: https://english.rvo.nl/sites/default/files/2020/07/National%20Climate%20Agreement%20The%20Netherlands%20-%20English.pdf. Also, what about adding information about the EU restoration law here and how this relates to rewetting etc.? This is however just a suggestion, not a “need to”.
2) Abstract, line 8: “Net Ecosystem Exchange (NEE) of CO2 demonstrated pronounced seasonal dynamics across different land-use types.” I would suggest to adjust this sentence and make the land use types the subject of the sentence. Different land-use types showed pronounced ...”
3) Line 59/60: “The causal diagram (Fig. 2) illustrates the interconnected controls of climate drivers, hydrology, and soil properties on peat oxidation in Dutch peatlands.” Is this the case for Dutch peatlands alone? Or is this working for peatlands more generally? If it is super specific for the Netherlands, would be worthwhile mentioning why this is the case. If it’s more generally applicable, I would point that out, because then a wider audience could use it.
4) Line 66: “This complexity makes it inherently difficult to formulate a general ERF,..” Is the trouble not also that one would need to have a lot of data? Considering that one needs to measure a lot of different elements to really get this interactions all accurately in an ERF?
5) Line 76-77: “As a result, ERFs inevitably smooth over much of the temporal variability and spatial heterogeneity that shape CO2 emissions, contributing to the observed non-linearity and site-specificity in groundwater–carbon relationships.” Is this really true? While ERFs based on annual or mean groundwater levels inevitably smooth temporal variability and spatial heterogeneity, it is not clear to me that this smoothing necessarily produces non-linearity.
6) Figure 3: In the caption, not all therms are explained (Fmanure etc. are not in there) I would make sure that all are explained.7) Line 133 – 136: “The eddy covariance (EC) monitoring network, including detailed documentation of data processing and harmonization, is described in a companion data paper currently in preparation. The machine-learning modelling framework is presented in a separate methodological manuscript, also in preparation.” Maybe you can add this to the Code and data availability section. I think the fact that data and code is not available makes the study less reproducible (at least during the review process and also during the period when readers do not have access to the code and data), but I hope tihs data will become available in due time.
8) Line 165 – section: Here, it would be probably good to mention if the same sensors were used for the mobile tower setup.
9) Figure 4: Although I generally like the figure, I suggest making the map somewhat larger and the station symbols slightly smaller, as this would make it easier to identify the locations of the EC towers. If colour is used to distinguish land-use types, I would also suggest using a consistent colour scheme for the same land-use categories wherever possible. At present, the large number of colours makes it difficult to obtain an overview of the spatial distribution of the different land-use types.
In addition, the current labels are not always very informative without referring back to the text. For example, labels such as “Fen meadow clay thin layer” and station codes such as “LAW_ICOS” do not immediately tell the reader which site is being referred to or what its main characteristics are. I suggest using a simple site identifier that can be directly linked to Table A, and explicitly providing this link in the figure caption. Alternatively, the stations could be numbered and the corresponding numbers linked to Table A. This would make the figure easier to interpret independently of the main text.
10) Line 299. 200: “Gaps greater than 60 days in length and gaps resulting from the mobile measuring strategy were not filled with the MDS algorithm; beyond this threshold, conditions at the time of the gap are too far removed from those of available look-up entries to yield reliable estimates, and the ML model described below is used instead”. I would adjust this sentence as follows (1) removed is probably not the right wording here, adjust this and (2) shorten the sentence or rewrite it into two sentence to make it easier to follow for the reader.
11) Line 203 – 204: “Missing meteorological data was filled with data from nearby NOBV stations and KNMI (Dutch meteorological institute) stations.” Here, it would be great if the authors could give some information on how close these stations are to the EC measurement towers.Table 1: Change “Depthof to “Depth of”.
12) Line 225 – 226: “Each dataset was first filtered for data quality and screened for outliers or inconsistencies”. Maybe the authors could add a sentence on the way this was done or refer to publications that have used the same filtering etc.
13) Figure 5: I like the graph, I think it gives a good overview of the workflow. I just have some small remarks to slightly improve the graph. In step 2 – at one arrow there is written “repeated 64 times”. It looks like the “repeated is written with a different font and it’s more tricky to read. Generally, in multiple cases the text is not really fitting in the boxes. I would propose to adjust the size of the boxes, so that it is easier to read it. In step 2, there is written “Partition in 3 weeks contiguous blocks for for LOO”. Should this not read “Partition in 3 weeks continuous blocks for LOGO”? In the text in step 2, I found several LOO, either this is an issue with the way I display the .pdf (Adobe) or the G is not printed here appropriately (or it should read LOO and I have not understood this).
14) Figure 6: I wonder whether the figure could be adjusted to make the main message of Section 3.1 easier to identify. At present, the large number of boxplots across the different 3-month periods and classes makes some of the broader patterns, such as differences in peak seasonality, relatively difficult to distinguish. One option could be to merge some of the classes in the main figure to highlight the broader patterns, while presenting the variability among the individual classes separately if this level of detail is important for the analysis. For example, one panel could show the main patterns using broader land-use categories, with an additional panel showing the individual classes. This might make the figure easier to interpret while retaining the information on differences between specific classes.
15) Line 197 – 198: “Sites with similar mean groundwater levels displayed markedly different NECB values, underscoring the influence of strong site-specific controls.” Here, I assume that the authors are referring to Figure 7. If so, please consider explicitly referring to the spread of NECB values at similar groundwater levels, for example at groundwater levels between approximately −60 and −40 cm in Fig. 7A.
16) Line 198 – 199: “Several pronounced deviations corresponded to sites underlain by a marine clay layer ... ”. Maybe explain here in an extra sentence why these deviations refer to the clay layer depth? Why this is so important here? I think this is important, because it makes it probably easier to understand for the reader without reading the paper by Nijman.17 Figure 8: I wonder whether the presentation could be adjusted to make the distinction between net carbon sources and sinks more explicit. While the figure provides information on NECB and its components, it is not immediately clear from the current presentation whether and where the peatland systems shift from a net source to a net sink of carbon, or vice versa.
This seems particularly important because such source-to-sink transitions are potentially among the most relevant outcomes of the study from a management and policy perspective. Relative changes are useful for evaluating the effects of different management practices, but the absolute magnitude and sign of NECB are also important for interpreting the actual implications of these changes. I therefore wonder whether the authors could make the zero line and/or the sign of NECB more visually explicit, or alternatively refer more clearly to another figure or analysis showing the absolute NECB values. This would help the reader interpret both the magnitude of the management effect and whether it results in a change in the overall carbon balance.
Citation: https://doi.org/10.5194/egusphere-2026-3151-RC2
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Summary: The manuscript titled “Groundwater-Level Response of Annual CO2 Budgets from a Dutch Eddy Covariance Network: Comparison with European Temperate Peatlands across Land Use and Sites” uses a large set of Eddy Covariance measurements, ground water level measurements and additional site information to relate net ecosystem CO2 exchange with hydrological conditions of peatlands in the Netherlands. The manuscript thus addresses an important topic in large scale emission modelling, land use transformation, emission reduction and agricultural policy. Herewith, the manuscript fits well to the aims and scope of EGUsphere.
The main findings of this manuscript are, that water level is only a weak predictor for peatland emissions, strongly impacted by site-specific conditions like land use and clay cover. Impacts of specific water management measures were characterized as ambiguous.
General comments:
The main concern about this manuscript is, that it is based entirely on large, but yet unpublished data sets, unpublished methods for green house gas measurements and gap filling routines, making it impossible to evaluate the quality of the finding presented. In some data sets, biases are introduced by the data acquisition and processing (dry dip wells, completely omitted incorporation of grazing into CO2 balances, although 10 sites out of 21 were dairy pastures). Sites were further misclassified by ignoring the actual state of the hydrologic conditions or vegetation cover. Some of the presented findings cannot be backed up by the data presented. Finally, the major outcome, that water level in peatland soils is only a weak predictor for its CO2 balance, is a strong claim and contradicting current process understanding in the vast universe of literature on this topic. If true, this requires a comprehensive discussion and plausible explanations, which the authors omit. Please see the detailed comments below.
Specific comments:
L 15: The correlation to summer water levels were nowhere shown in the manuscript nor discussed.
L 34: The most obvious measure, restoration, is omitted from the discussion. It would be valuable for the reader if the national context of restoration, e.g. in conjunction with the upcoming demands of the EU restoration law, would be discussed as well. It would be valuable to know in the context of this paper, if the Dutch government is not taking into account this land use for peatlands in its national strategies.
L 42: Here the authors state, that ground water management plays a crucial role in peat degradation and emissions, which they clearly contradict in their findings. Please clarify that.
L 50: “…, whereby capturing emissions caused by deeper soil drainage is the primary motivation for introducing this non-linearity.” This sentence is not clear to me, as you state in the next sentence, when using non-linear functions, emissions from deeper soil layers are smaller (since not the same amount of oxygen can reach down there as a result of diffusion through the reactive porous media, compared to upper layers). Please make that clearer.
Fig 1: It is not explained how you calculated “effective linear slope”, is it the arithmetic mean slope between the given intervals? If so, state clearly.
Fig 3: The sentence “NEE measured by eddy-covariance integrates plant-driven fluxes…” omits a closing bracket, leaving unclear which fluxes are considered plant- or peat-based, in particular short-term microbial respiration. Further, the explanation omits peat based fluxes from all upper layers, e.g. the root zone, since only peat oxidation “from deeper degraded pools” is mentioned, leaving this description unclear if not highly misleading. According to this figure, no long term peat oxidation occurs in the root zone, which is incorrect.
L 90: Lateral exports were estimated only at fully inundated sites and set elsewhere to zero. Although it is desired to use all available data at hand, this introduces an artificial bias when comparing NEC balances among sites, rendering these comparisons corrupt. Please treat lateral fluxes the same way for the purpose of site comparisons. Further, Appendix F details that the impact of grazing on NECB was fully ignored in this study, although 10 sites out of 21 were dairy pastures. This further adds to erroneous site comparisons.
L 96: The no-accumulation assumption of pastures is valid here for annual, and even more, multi-annual balances and in line with international standards, e.g. IPCC guidelines. These could be cited here to back-up this assumptions.
L 101: “The addition of manure might imply the addition of carbon to the system..” The addition of manure is always an addition of carbon to the system.
L 132: The entire data analysis is based on large, but yet unpublished data and the data (e.g. flux and water level time series) is not at all shown or discussed in this paper. Thus, the quality of the underlying data remains completely unknown. This strongly violates established scientific practice and the standards of EGUsphere, giving rise to possibly tremendous misinterpretation of the data.
L 140 / 165 / 200: The new approach of using intermittend mobile eddy towers is not an established scientific strategy for conducting tower-based flux observations, due to the resulting, extremely large data gaps. This method was not published or validated befor this manuscript, similar to the newly proposed, ML-based gap filling method. Thus, this manuscript, similar to the underlying data sets, relies on unpublished methods, questioning the quality of the outcomes.
L 249: Water levels exceeding this range (0 to 1-1.5 m) were recorded at the installation depth limit. This means, that whenever the water level fell below this value, recorded values were set to e.g. 1 m. This of course introduces a bias in the annual mean water levels (towards higher water levels). Were dip wells deepened after data retrieval discovered this incorrect installation to reduce this type of bias? Why were these times not filled with more realistic values, e.g. by some ML algorithm as the authors apparently are used to these types of methods? This artificial bias could substantially lower the correlation strenght to emissions and need to be elaborated, since this is one of the main outcomes of this manuscript, and also making non-linear behaviour more likely in fig 7, altering the NECB=0 intersection.
L 280: The authors state, that the vegetation composition of the Sphagnum site (ILP_PT) was in the early state of establishment an resembles more of an extensive grassland. Attributing the flux results to Sphagnum paludiculture is thereby wrong and incites erronous interpretation by the reader. The authors should either name the site properly reflecting its conditions, e.g. semi-natural grassland, or remove it from the analysis. The authors need to make sure to use an appropriate classification and naming as well for all other sites. See also caption of Fig 6: “Sphagnum-based paludiculture is comparable to extensive grasslands”, this a strongly misleading and false statement. See also Fig 7, which shows a wet pasture, but with an annual mean water level of -50 cm?
Fig 6: Authors attribute the reduced summer emission balances at sites with a clay cover to reduced peat oxidation. This claim is nowhere backed up by, e.g. biomass data, since a reduced biomass growth on these sites could also be a cause with the same impact on the seasonal balance, bearing the strong risk of mixing fossil peat emissions with recent biomass turn-over.
Fig 7: How do the authors explain net uptake or near to neutral emissions at deeply drained sites, since no other synthesis publications like Evans et al., (2021) or Tiemeyer et al., (2020) show this behaviour. This strongly contradicts current process understanding.
L 294: As it is also common in the field (see Table 2), was there ever a non-linear function tested against the presented data set, e.g. parabolic or compertz, to see if this dependency would yield a better representation of the data than a linear one and thus increasing the likelihood of a more realistic process understanding? Otherwise, the conclusion of weak correlation of NECB to WLEV could be a matter of choice instead of inference.
L 311: Section 3.4, set out to display outcomes with relation to Land-use and management, consists of just two sentences and seems thus, fairly incomplete. Maybe some text went missing during the writing?
L 316: Section 3.5 is set out to display comparisons between pairs of control and treatment sites. However, may be because the entire section is just two sentences long, it omits completely to explain the different treatments, e.g. what is the difference between the ALB_RF and the ALB_MS sites. I could not find it in the entire manuscript nor the appendix tables. This should be part of the Methods section, however, the site description part there is also only 4 sentences long. Conclusively, with out the necessary information the entire control-treatment comparison remains pointless.
L 333: This important claim cannot be backed up by data in this paper, since the observed annual mean water levels often violates the given land use classification (see comment to Fig 7.) and the range of water level changes in Fig 9 (~25 cm) is way to small to conclude findings on saturation effects (in the wet or dry range) given the actual range observed (~80 cm, compare Fig 7).
L 351: Have the authors taken into account the uncertainty behind all slope values given, when comparing their outcome with previous studies? If done so, is a significant distinction even possible or are the majority of slopes so close, that they can not be distinguished from one another?
Table 2 and Fig 10, 11, 12: It is unusual to present data outside the result section (like here, in the discussion). This way, there is no place to thoroughly describe these findings in detail there, and the necessary background for the reader is missing at this point. Please move Table 2 and Figure 10, 11, 12 into the results section.
L 388: Here you state, that you have fitted various slopes, apparently for different land use types, however, in the entire manuscript, there is just the fit over all sites given (Fig 7.). Were these additional fits not included into the manuscript? Why have these never mentioned before?
L 398: The authors derive the conclusion, that type of measurement (e.g. Eddy Covariance vs. chamber) is likely to contribute to observed differences in data sets. This conclusion cannot be derived, since reported EF, as they state themselves, strongly depend on various site conditions as well as the specific site selection included in each data set. Given this variability, systematic differences between measurement techniques cannot be derived. Which the authors state themselves further down in L 405.
L 412: The authors speculate, that biomass removal impacts NECB, in this case of restored and paludiculture systems. From Eq. 1 and Fig 8, this should rather be a derived outcome of this paper (the authors take biomass export into account), than a guess. Why where the authors unable to derive that conclusion based on their data?
L 426: See comment to L333. Additionally, the authors showed differences in observed water levels among the different country specific studies. Consequently, in each country, e.g. “deeply drained” refers to different water levels. To guarantee a comparability, the authors need to use absolute values instead of inconclusive terms.
L 427: See comment on L 412.
L 445: The authors present the water level as a weak predictor for NECB, omitting that they characterized it as the first-order descriptor (L 363), omitting a better predictor available for large scale modelling or mentioning the vast universe of literature identifying water level as the main driver for emissions from peatlands. This appears to be a biased opinion rather than an objective assessment.
Technical corrections: None