Throughout the years, these systems have been described in various ways. E.g., Querner et al. (2012) call them subsurface drains, Weideveld et al. (2021) call them subsoil irrigation and drainage systems, Hoogland et al. (2020; DOI:10.5194/piahs-382-747-2020) refer to them as drain infiltration, and Hoekstra et al. (2020; DOI: 10.5194/piahs-382-741-2020) favor pressurized drainage for a system similar to that on the Assendelft site. So why coin yet another name instead of using (parts of) a previous one, especially when the new name is less concise? Subsurface (and/or subsoil) seems superfluous: where else would the drains be? And submerged is not accurate all the times: a part of the appeal of these systems is that after a heavy rain shower, you can use them as conventional, non-submerged drains to more rapidly drain a field. Would (pressurized) drain irrigation systems not suffice?
We thank Henk van Hardeveld for his critical look and thoughtful comments that will improve the quality and readability our manuscript. Especially the comment on featuring more prominently our novel method to estimate peat respiration and the comment on highlighting the quantitative comparison with previous studies will both certainly raise the impact of our study. We are happy to apply revisions to improve our manuscript as formulated in the answers to the referee comments (RC1-RC7) in the .pdf that is attached to this reply.
Two questions regarding your aim. First, a minor technical point, can you try to state your aim without using brackets? Surely, every part of your aim must by definition be important? Second, more importantly, can you try to allign your aim and your narrative more closely? I think the most important legacy of this paper will be that you introduce a novel method to more accurately assess the impacts of water management strategies on peat decomposition and greenhouse gase emission. So, must your new approach not take central stage? in your aim you mention various strategies, hydrological settings and meteorological conditions. But this strikes me as merely an afterthought. Once you have designed a better approach, by definition it will allow you to betrer explore the effectivity of strategies in different settings. It is nice that you do, don't get me wrong, but I think its is merely to demonstrate the added value of your approach.
In addition, please focus your Introduction on the processes that your approach addresses, avoid too much focus on anecdotal case studies such as you decribe in line 80–85, using vague phrases like "was suspected" and "the authors think". You might be aware that there has been much controversy about drain irrigation systems, sparked by a paper in bulletin 2018-06 of the International Mire Conservation Group. Arguably, the essence of this "knowledge war" is about a wide range in observed effectivities of these systems, and the question to what extent it is valid to use estimations based on water tables to estimate their effectivity. You method may help to settle this debate. For instance, in line 581–588 you make a strong point by using your method to explain why previous case studies in various settings come up with different conclusions.
Moreover, as your method might pave the way for better impact assessments, the comparison with previous methods should be better addressed in the Introduction section. I think Section 4.4 is one of the hightlights of your work, yet the previous methods are only discussed in very general terms in line 87–91.
I like this part of your approach, but please explain it more clearly. Fig. 4 is featured quite prominent, but the shapes seem random. I suspect this is not the case, that you have designed several categories. You merely state that they are "loosely based on the shape found by Säurich et al. (2019)". Can you elaborate on that? Especially because "the" shape of Säurich et al. (2019) does not exist. They present a wide variety of shapes and also mention that the variety would have been even bigger if they had included shapes found by other research.
I strongly suggest that you analyze the sensitivity of your assessment.
Part of the controversy surrounding methods to assess the impacts of water management strategies in peatlands centers on their validity range. E.g., are methods derived on sites without drain infiltration systems also valid for sites with drain infiltration systems? If your method is to rise above such controversy, you cannot suffice by stating that your model simulates the water table dynamics "reasonably well" (line 318), or that the modelled temperatures were merely "slightly too high" (line 337). According to the approach of Van den Akker et al. (2008), a 20 cm offset in the summer water table may cause up to 60% extra emission. And assuming a Q10 of 2–3, a 1.45 °C offset in temperature may cause a 10–17% increase in microbiological activity. This raises the question to what extent you can accurately choose which WPFS optimum curve to use in your model? You have chosen shape 16, with a correlation of 0.591. But shape 8, which seems highly improbable has an almost similar correlation of 0.590.
Regardless of the results of your sensitivity analysis, I believe your approach will be a step forward compared to the current water table based approaches. But I do like to know just how robust your method is. Will a slight offset in your hydrological model or the chosen shape of the WPFS optimum curve produce similar, of very different results? And in case of high sensitivity, what is needed to accurately pinpoint which WPFS optimum curve to use? Multiple years of monitoring results on multiple sites, perhaps? In other words, are we there yet? Or are we merely still moving towards a better approach?
Can you elaborate on the potential respiration rate? How do you explain that Reco for the sites with and without irrigation drains are quite similar, but the potential respiration rate is much lower at the site with irrigation drains than at the control site? And how do you explain the sharp drop in potential respiration rate in September that is not matched at all by the measurements? It seems the drop can be related to high modelled water tables and the chosen WFPS optimum curve with zero activity at WFPS = 1. How do you interprete that?
Technical question regarding Fig. 6 (a): can you better explain which lines are plotted on which axes and add units to the third axis?
Suggestion: can you also show these graphs for the Vlist site?
Arguably, the results for the Assendelft and Vlist sites are quite different. So it would seem pressurized irrigation drains and regular irrigation drains are two quite different systems, with different potential respiration rates in similar settings. Can you distinguish between both categories in the Figure? Currently, it is unclear which dots may refer to a pressurized system.
The comparison between your approach and previous methods is very valuable. But the chosen relations seem a bit random. On the one hand, the relation of Fritz et al. (2017) was found in a semi-scientific Dutch magazine, which is only accessible by sending an e-mail to the authors. On the other hand, the often used relation of Couwenberg et al. (2011; doi.org/10.1007/s10750-011-0729-x) is lacking. As is the often used relation of Van den Akker et al. (2008), which uses the average summer water table, which in line 622 you claim is better than the average annual water table such as used by the chosen relations. Your comparisons will make a stronger point if you include those relations as well.
Technical comments: please explain what the dots in Fig. 11 are, change the units of the x axis of Fig. 11 and Fig. 10 into m below surface, and change the caption of Fig. 11 (in a concise manner) to match everything that you present.
Carbon fluxes from drained peatlands receive increasingly attention within various scientific disciplines. This paper follows this trend promoting an interdisciplinary approach. The authors have provided a valuable theoretical attempt to improve the community’s understanding of soil moisture and carbon fluxes interactions. At the first sight the modelling work focuses on combining soil moisture, temperature and potential carbon mineralization rates for an improved quantification of hydrological variables steering seasonal peat losses.
However, after a second read through there is more to the paper. The authors incorporate a new method to approximate carbon fluxes from drained grasslands on peat quantitively. The new method relies on closed chamber technique. Chambers were supposed to close automatically 2-3 times per hour. The static chambers are reported to be surprisingly high (full 20 inches).
To compare the new chamber method with published data the authoring team builds a soil-water-carbon model. The 3.5 model exploration (Figure 1) helps to quantify how well the flux method can approximate existing carbon flux data at an annual resolution. Figure 11 highlights that the gas flux method deployed for model calibration in this study may systematically underestimate carbon fluxes from drained peatlands. The comparison with Evans et al. 2021 seems vulnerable given the almost absent overlap in grazing intensity and primary production of the sites included in both data sets.
The paper’s modelling approach would need a proper cross validation with more established gas flux methods on the one hand and multi-year data sets for calibration and validation on the other hand. Multi-year carbon flux data sets are essential for quantifying main drivers of soil carbon, climate and water interactions in peatlands (e.g., https://doi.org/10.1111/j.1365-2486.2006.01292.x https://doi.org/10.1111/j.1365-2486.2009.02104.x ). More so where soil temperatures are likely to change methodically by static chambers that are commonly deployed for experimental warming at higher latitudes.
The title seems misleading. All 4 paddocks remained drained during the course of the experiment. ‘Cutting peatland CO2 emissions with irrigation measures’ would fit the content of the paper.
I enjoyed reading this version of the manuscript. Looking forward to updates of the model supported by cross-validation of carbon fluxes.
We thank you for your critical reflection and the discussion points you brought up and are content to read that you evaluate the research as a valuable approach. We discussed your concerns with the team and are motivated to improve the manuscript as explained in the answer formulated below.
You mention that our method to estimate peatland carbon fluxes relies on the closed chamber technique. Our aim was to measure CO2 fluxes with the least amount of soil and vegetation disturbance as possible. The height of the chambers is above the maximum vegetation height. Smaller chambers would not support the conditions that we find at the farmland. Furthermore, we are aware of affecting the microclimate of the soil and vegetation, with possible changes in air temperature, amount of wind, radiation, precipitation and air moisture content. Therefore, we chose not to compare model outcomes with the absolute observed CO2 fluxes, but we chose to compare CO2 flux-differences between different management regimes. Furthermore, we compared our measured chamber ecosystem respiration dynamics with potential aerobic respiration rate dynamics that we calculated with a variety of WFPS-activity curves. We chose the WFPS-respiration activity curve that matched the dynamics the closest. An under or overestimation in chamber ecosystem respiration would not have any consequences for this comparison, as we solely rely on the daily and seasonal dynamics. We stimulate air mixing by using ventilators and change the location of the chambers every two weeks to limit the development of a micro-ecosystem and to achieve proper field representation. Our equipment has been tested in the lab and is calibrated each year.
We think that the chamber flux data that we used in our yearly carbon budgets give reliable estimates of the effects of different peatland management practices. Firstly, we found that our model supports our measured differences, as we found a similar reductions in yearly carbon budgets -that were constructed using the chamber measurements- as our model simulated for both our measuring locations. We did not calibrate our model on these differences but used literature and measured properties to describe soil water and temperature. Secondly, the research application of static automatic transparent chambers to measure greenhouse gas fluxes knows a long history and has been evaluated successfully frequently (Huth et al., 2017). Many published research articles are based on chamber datasets with highly limited measuring intervals and continuity (for example Görres et al., 2014; Tiemeyer et al., 2020). Interpolation is done with relatively simple light and temperature response curves, resulting in large uncertainties in the yearly carbon budget. In contrast, our temporal data coverage is very high (>90%) and interpolation is hardly needed. Following your comment, we stress reliability of transparent chamber measurements by referring to research articles in which comparable chamber methodologies were used to quantify CO2 fluxes with similar vegetation settings within our revised manuscript.
Indeed, it would be great to be able to present a multiyear cross-validation between chamber and eddy-covariance measurements. However, it has been already been proven that eddy-covariance and chamber measurements yield comparable results (Frolking et al., 1998; Laine et al., 2006; Stoy et al., 2013). Besides this and the arguments that we provided earlier -to explain why we can rely on the chamber measurements- the peatland community is in need of knowledge on how to prevent greenhouse gas emissions from managed peatlands. We are currently processing eddy covariance and chamber data of 2021, and plan to publish the outcomes of the comparison. Nevertheless, this should not constrain the publication of this research article. As a matter of fact, eddy covariance also induces many uncertainties (affected by choices in measurement set-up and methodologies for analysis).
We regret to read that our title could be misleading and will consider alternative options for the term rewetting. However, only referring to irrigation measures in the title as you suggest would miss the ditch water level elevation measure to reduce peat respiration.
We agree upon the fact that extensively used grasslands are underrepresented in the research of Evans et al. (2021). However, the authors state that annual groundwater levels “override other ecosystem- and management-related controls on greenhouse gas fluxes”. Therefore, we think that the comparison with Evans et al. (2021) within our research is appropriate. Nevertheless, we included other important relations between annual water table depth and CO2 emissions. Within our revised manuscript, Figure 11 will be updated with the relation from Couwenberg et al. (2011). Following your comment we will consider in text comparisons featuring the other relations plotted in Fig. 11 instead of highlighting the comparison with Evans et al. (2021).
Frolking, S. E., Bubier, J. L., Moore, T. R., Ball, T., Bellisario, L. M., Bhardwaj, A., Carroll, P., Crill, P. M., Lafleur, P. M., McCaughey, J. H., Roulet, N. T., Suyker, A. E., Verma, S. B., Waddington, J. M., and Whiting, G. J.: Relationship between ecosystem productivity and photosynthetically active radiation for northern peatlands, Global Biogeochem. Cycles, 12, 115–126, https://doi.org/10.1029/97GB03367, 1998.
Görres, C. M., Kutzbach, L., and Elsgaard, L.: Comparative modeling of annual CO2 flux of temperate peat soils under permanent grassland management, Agric. Ecosyst. Environ., 186, 64–76, https://doi.org/10.1016/j.agee.2014.01.014, 2014.
Huth, V., Vaidya, S., Hoffmann, M., Jurisch, N., Günther, A., Gundlach, L., Hagemann, U., Elsgaard, L., and Augustin, J.: Divergent NEE balances from manual-chamber CO2 fluxes linked to different measurement and gap-filling strategies: A source for uncertainty of estimated terrestrial C sources and sinks?, Zeitschrift fur Pflanzenernahrung und Bodenkd., 180, 302–315, https://doi.org/10.1002/jpln.201600493, 2017.
Laine, A., Sottocornola, M., Kiely, G., Byrne, K. A., Wilson, D., and Tuittila, E. S.: Estimating net ecosystem exchange in a patterned ecosystem: Example from blanket bog, Agric. For. Meteorol., 138, 231–243, https://doi.org/10.1016/j.agrformet.2006.05.005, 2006.
Stoy, P., Williams, M., Evans, J., Prieto-Blanco, A., Disney, M., Hill, T., Ward, H., Wade, T., and Street, L.: Upscaling tundra CO2 exchange from chamber to eddy covariance tower, Arctic, Antarct. Alp. Res., 45, 275–284, https://doi.org/10.1657/1938-4246-45.2.275, 2013.
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Studies on the rewetting impact on the carbon dynamics of used peatlands are of great importance, because there are still large knowledge gaps and contradictions in this regard. Moreover, solid knowledge on this is a key prerequisite for the development of effective measures to revitalize peatlands and mitigate human-induced climate change.
However, due to fundamental shortcomings, this manuscript unfortunately cannot contribute to clarifying the aforementioned deficits and challenges. In particular, this is due to the following substantively interrelated issues.
- The authors fail to demonstrate the link between the so-called potential microbial respiration they simulate and the real mineralization of peat. This starts with the lack of a clear definition for this term. Second, they did not verify whether the data used for simulation from third-party laboratory experiments even reflect the behavior of the peat substrates studied here. This is because it is well known that the chemical properties of peat (peat quality) play a major role in determining its decomposition kinetics (e.g., Leifeld et al., 2012: Sensitivity of peatland carbon loss to organic matter quality. Geophys. Res. Lett., 39, p. L14704). Third, the comparison of simulated potential microbial respiration with measured ecosystem respiration made here is also not meaningful because neither the actual proportion of possibly congruent heterotrophic respiration in ecosystem respiration as such is known, nor whether it does not change significantly in the course of plant development or multiple grass cutting. The latter is very obvious (Fig. 6), but, as mentioned, has not been verified.
- As a proxy, so to speak, in lieu of not calibrating and validating the model with real data on peat mineralization from their own and other researchers' field plots, the correlative relationships between the simulated potential respiration rates and the measured components of a C budget were used. However, the authors ignored the point that the factors used in the model, soil temperature and, most importantly, WFPS, were determined by the groundwater level in the same way as all components of the C budget (Fig. 5a-c, Tab. 4, Fig. 10). In other words, all the results obtained on the intensively used peat meadows studied here were controlled by the groundwater level in the same way, i.e., they were not independent of each other. Therefore, contrary to the authors' claims, the close correlative relationship between the components of the C budget and simulated potential mineralization is not evidence that their simulation approach can be used to determine the success of rewetting more precisely than conventional analysis of the relationships between groundwater level and the C budget.
Therefore, the novelty value of the presented studies with respect to the climate impact of rewetted peatlands and factors relevant in this context is very low. It would have made much more sense if the authors had focused on elucidating the role of other factors that are also important in this regard independently of the groundwater level (e.g., nutrient supply, type and productivity of vegetation, duration of rewetting). This is because there is only fragmentary information on this so far.
In view of this, I recommend rejection of the manuscript.
However, this does not mean that the results on the influence of the SDSI approach on the C-dynamics and the C budget in combination with hydrological modeling cannot be published in a newly designed manuscript after all. But that is not reasonable until the results of at least three years of monitoring are available.
We thank the reviewer for her/his time to read and review our submitted manuscript. We -as authors of the article- feel that we have made fundamental progress in understanding the effects of rewetting measures in agricultural drained peatlands on peat mineralization. We explore, with a model and previously published relationships between peat mineralization and soil moisture and -temperature, the predicted mineralization reduction by raising ditch water levels and applying subsurface irrigation: the two most discussed water management measures for reducing peat mineralization in the Netherlands. We show that the degree of expected reduction strongly depends on regional hydrologic setting and weather conditions during the year. Moreover, we show that the now widely used indirect relationship between average groundwater level and mineralization to predict emissions from peatlands is likely to be different for raising ditch surface water levels and applying subsurface irrigation, due to contrasting interplay between groundwater level, soil temperature and soil moisture between both measures. The latter is a hugely relevant result. Without this insight we now likely overestimate the reduction effects of subsurface irrigation. In addition we show that some locations are expected to be more suited for certain measures than others, which provides guidance on where to first apply these measures. Therefore, it was a disappointment to read that the reviewer did not see these merits and instead focused on aspects that were not studied or asks for longer datasets that do not fit the timeframe of our research.
First of all, the comments of reviewer 2 about the circularity in our reasoning made us realize that we need to sharpen the objective and structure of our paper. The objective of our paper is to explore the expected effects of raising surface water tables and applying subsurface irrigation, by integrating literature relationships between peat mineralization and soil moisture/temperature into an advanced groundwater flow, soil moisture and soil temperature model (HYDRUS). To our knowledge, we are the first to publish such an approach and explore the effectivity of water management measures over a range of environmental settings. We corroborated our modelling results with one year of measured datasets at two contrasting locations. This is indeed, as the reviewer mentions, not enough to calibrate and validate the model components or gain fundamental new insights in small scale soil processes. However, it is enough to show that our modelling results with parameters derived from literature are realistic on the field-scale and that we can confidently explore the effects of the proposed measures on the emission of agricultural fields.
Secondly, reviewer 2 misunderstood our definition of potential microbial respiration rate and how this term relates to actual/real mineralization. We agree with the reviewer that our manuscript should be improved with a clear definition. Potential microbial respiration rate is the fraction of the maximum amount of microbial mineralization rate from a particular volume of peat. When studying the effect of water management measures on peat decomposition at a particular location we assume that the properties of the soil profile (including quality of the organic matter) remain similar. In fact, the potential mineralization of the peat substrates that were included within our research has been measured in the laboratory, as opposed to the claim of the reviewer that we did not verify the data used for simulation. It was found that maximum mineralization rates on the control and SSI parcel were similar, and that the variation in the maximal mineralization rate of five different intensively used lowland fen (meso- eutrophic) peatlands was low. Therefore, we can safely use the maximum mineralization rate as we define it. When discussing recently drained or bog (oligotrophic) peatlands (that were not included within our study), this maximum mineralization rate might differ. Within our revised manuscript, we will elaborate upon this line of reasoning.
Thirdly, we understand the concerns of the reviewer about the comparison of the modelled potential microbial respiration rate and Reco in Fig. 6 (Sect. 3.4.1). In the section we mention that we are very aware of the fact that this Reco includes plant respiration which is influenced crop development/harvesting. Unfortunately, no exact methodology is available to disentangle various forms of respiration (peat respiration, plant respiration, respiration of root exudates, respiration of dead plant material – fractionation of young and old carbon). At the moment, our team is researching these contributions to respiration, but these results are beyond the scope of our paper. However, we did not use Reco to invent mineralization dependency on soil moisture, but we used results that were found within laboratory studies of Säurich et al. (2019) to define this relationship. We cautiously interpreted the general shape of published datasets of lab experiments and presented 16 relations that mostly consist of this shape. Consequently, we selected the curves that explain most of the variation in observed Reco. Even though we know that plant respiration could be influenced by soil moisture, the foundation of our methodology is based on laboratory studies reported in literature. Therefore, the Reco is less important than reviewer 2 argued. As reviewer 1 also commented on this approach we will explain this with more detail and include a sensitivity test evaluating also the other curves.
Fourthly, reviewer 2 mentions that it is problematic that soil moisture content is related to the groundwater level. Although the two variables are indeed strongly related, soil moisture is a more sophisticated measure of groundwater hydrology and is represented by precipitation dynamics, evaporation and water retention characteristics. Unlike the groundwater level, soil moisture varies with depth, and this adds an extra dimension to the estimation of peat mineralization in comparison to using the groundwater level alone. Therefore, we do not understand the claim of reviewer 2 that there is a disadvantage in using soil moisture dynamics as compared to using the groundwater level when estimating peat mineralization.
Finally, the reviewer suggests that our method to estimate (potential) peat mineralization would not give better results than standard relationships with C-budget (C-loss) and groundwater level. It is remarkable that the reviewer promotes (average) groundwater table height as predictor for peat mineralization, while we know that this predictor falls short -as mentioned in the introduction of the manuscript and as shown by our results (Fig. 10, 11). In fact, both the standard approach and our approach are a strong simplification of the many outcomes we may encounter in the field. The reasoning of the reviewer supports a one-sided view on the effectivity of water management strategies to reduce peat mineralization. As a consequence, there is a risk that water management strategies are less effective than previously thought or that they may even have adverse effects. The view of the reviewer on standard relationships between peat mineralization and groundwater level is exactly the view we attempt to nuance with our research: Yes, creating wetter conditions limits peat mineralization, but if we take both soil moisture and soil temperature into account the expected reduction by subsurface irrigation is not as large as expected from groundwater levels alone. This needs to become clear and needs to be taken into account in national greenhouse gas budgeting (i.e. budgets that need to be reported within the European Climate Monitoring Mechanism).
In summary, we think the second reviewer did not fully grasp the objectives of our paper. With the proposed improvements in reply to the comments of reviewer 1 & 2 we think we can substantially improve our manuscript and that it will become a valuable and innovative contribution to the discussion on rewetting measures in agricultural peatlands. We look forward to getting this opportunity.
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