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.

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).

References

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.

Tiemeyer, B., Freibauer, A., Borraz, E. A., Augustin, J., Bechtold, M., Beetz, S., Beyer, C., Ebli, M., Eickenscheidt, T., Fiedler, S., Förster, C., Gensior, A., Giebels, M., Glatzel, S., Heinichen, J., Hoffmann, M., Höper, H., Jurasinski, G., Laggner, A., Leiber-Sauheitl, K., Peichl-Brak, M., and Drösler, M.: A new methodology for organic soils in national greenhouse gas inventories: Data synthesis, derivation and application, Ecol. Indic., 109, 105838, https://doi.org/10.1016/j.ecolind.2019.105838, 2020.

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.