Review report, egusphere-2022-1424

The paper addresses a very important and timely research question, i.e. the CO2 balance of drained forested peat soils. The CO2 emissions from drained forested peat soil receives currently a very strong attention in many countries. Accurate and precise methods to estimate the soil CO2 fluxes, as well as the full ecosystem level CO2 fluxes are urgently needed.

The overall approach is statistical modelling with the main data input from the national forest inventory and meteorological data and parametrization based on empirical data on litter production as well as decomposition of different main components from dominating plant functional types.

The main results is that forested drained organic soils in Finland represents source of CO2 and that the total soil CO2 emissions from these soils have increased from 1.4 to 7.9 Mt CO2 for the period 1990–2021. Accounting for the entire ecosystem, i.e. also including photosynthesis and calculated for the whole country, forests growing on drained peatlands were a net sink of 0.2 Mt CO2 in 2021, i.e. close to C neutral.

The paper is an important contribution to a science based ground for accessing the land-atmosphere CO2 balance of forested drained organic soils.

Answer1: Thank you for the positive evaluation of the importance of our paper and the following comments that greatly help in improving the manuscript.

My major concern is that critical validation of the method is missing. The authors have made an extensive comparison with other emission factors. Still I am missing comparisons with direct measurements for a few example systems representing dominating types and climate settings. It is not an easy task, still urgently needed.

Answer2: The reviewer raises an important question on the validity of the proposed method. A method for GHG inventory should produce anaccurate 30-year emission time series on country-level. The sole reason why this manuscript was written is that, so far, such a method for forestry-drained peat soils has not existed To validate the results of our new method, we would need an independent, reliable country-level 30-year time series for comparison. However, the current/previous knowledge consists of Tier 1 and Tier 2 emission factors onlyand we do not have alternative time series to compare with. We totally agree with the reviewer that such comparison would be valuable; but it is a task that requires another study and a whole article of its own. There are no long measurement time series available, and what we would need are time series for tens of sites to compare the country-level consistency. Here we can only compare to Tier 1 and Tier 2 emission factors to see if the emissions based on our method are comparable to emission factors used in other GHG inventories.

Yet, all this said, it is important to realize that the main components of our method have already been extensively evaluated as the method we propose is based on litter production and decomposition estimation methods that are largely published (as cited in the manuscript). Yasso is also widely used and has been extensively tested and calibrated with large datasets. Finally, the core idea of our method, the estimation of soil CO2 balance as a difference between decomposition and litter production has previously been applied in forestry-drained peatlands in Ojanen et al. 2013 (http://dx.doi.org/10.1016/j.foreco.2012.10.008), Ojanen et al. 2014 (http://dx.doi.org/10.1016/j.foreco.2014.03.049), and Uri et al. 2017a,b (http://dx.doi.org/10.1016/j.foreco.2017.05.023; http://dx.doi.org/10.1016/j.foreco.2017.04.004) and its applicability discussed/tested in Ojanen et al. 2012 (http://dx.doi.org/10.1016/j.foreco.2012.04.027). Thus, we think that even though the method we suggest cannot here be validated as a whole, its components are in general well established and trustworthy.

In the revised manuscript, we will address this topic more in the discussion to ensure that we have clearly stated what validation has been done, what cannot currently be done and what should/could be done in future studies.

Also the current version of the abstract is hard to digest. It currently require that the reader has read the full article before reading the abstract. Please see detailed comments on the abstract.

Answer3: Agreed. We will simplify and reorganize the abstract. For instance, the annual emissions and removals of CO2 will also be presented per unit area (ha) where appropriate.

Detailed comments:

L 15   Discharge C export needs at least to be considered and potential bias if not included must be discussed. Necessarily not in the discussion section

Answer4: Agreed. We will mention dissolved C export in the rewritten abstract. The issue will also be elaborated in Discussion.

L15    conceptually I agree that the soil C balance is made up by just by above- and below- ground litter input and heterotrophic (saprotrophic) CO2 respiration. AND possibly also discharge C-export.  It is though important to clarify why autotrophic root respiration is excluded.

Answer5: Agreed. We will better explain why autotrophic (root) respiration was excluded in the original measurements. The issue is now briefly mentioned on L84.

16-17   Reformulate. Peatlands drained for forestry release CO2 even if the WT is not change. The change in WT due to drainage and forest ET may change the soil CO2 flux but also non-drained peatlands release soil CO2.

Answer6: We will state that the drainage increases aerobic decomposition and CO2 release.

L 20   here it is absolutely necessary that you clarify that the CO2 flux you model emanate from saprotrotrophic CO2 production only. Not stating this explicitly will confuse many readers.

Answer7: We will state in the abstract that we talk about “heterotrophic decomposition” and “annual heterotrophic CO2 release”, and in the methods explain why and how autotrophic (root) respiration was excluded in the original measurements.

L 24   do not understand. How is “harvested” trees included?

Answer8: We will better explain the data source of loggings and harvesting residues in the revised abstract.

L25    what area is the CO2 emission representing? Is it total or per unit area? I would very much prefer first presenting per unit area, e.g. m^-2 or ha^-1 and then areal totals. Currently it is very confusing.

Answer9: Good point. In the revised abstract, we will also present the emissions per unit area Figures 5, 6 and 7 already show the emissions per unit area for the time series.

L25    “1.4 to 7.9 Mt CO2”  You must add time unit, i.e. yr^-1.

Answer10: Units will be completed as suggested.

L27    is this totals for northern and southern Finland or what?`

Answer11: That is correct, the values give total emissions for southern and northern Finland per year. We will more clearly specify that throughout the text.

L28    what about the forest floor PFT´s contribution to CO2 uptake. It can be substantial. If it is not in your data it must me clearly stated that its contribution is so small that it can be neglected, which I really doubt.

Answer12: The contribution of forest floor vegetation is present in above and below ground litter production models which combine herbaceous plants, dwarf shrubs and mosses (Tables 5, according to Ojanen et a. 2014), excluding the fine root litter of dwarf shrubs, which  is included in “arboreal fine root litter”.

L25-30            this result section is very confusing. I suggest presenting both unit area based estimates (also adding the time unit (yr^-1)) and areal totals

Answer13: Agreed. The abstract will be simplified and rewritten.

L49    In the abstract you state an annual drained peatland soil CO2 flux during 2021 of 7.9 Mt and in the introduction state 3.8 for 2020. Thus you need to be specific in the introduction and clarify that according to method xx the annual peatland soil CO2 during 2020 was 3.8 Mt

Answer14: Agreed. We will stress that these results are from different methods.

L63-63            does these references really refer to saprotrophic CO2 flux, NOT including ANY autotrophic respiration. It is very important that you make this very clear. As “soil CO2 flux” normally includes also the autotrophic root respiration I think it is very important that you make it very clear in all of the text what you actually include.

 Answer15: We will check this and more explicitly state that only saprotrophic (heterotrophic) respiration is included in our method. Although already mentioned in the methods, this fact will be more explicitly specified. Ojanen et al. (2010) installed collars 6-12 months prior to their measurements so that live root connections got eliminated prior to their R_H measurements. It has been shown that roots die in trenched plots kept clear of vegetation within one year.

L80    “…. by the old method”  You must add reference after this statement

Answer16: Reference to National Inventory Report (2022) will be added. Also, the chapter that describes the old method will be revised and more details on its assumptions will be given.

L 87   C  mass input

Answer17: Expression will be completed as suggested.

L 91   think the sentence “Negative values denote net removal of CO2 from the atmosphere” is confusing. While a forested peatland represent a net removal from the atmosphere depends on the entire system (ecosystem) and not just the soil.

           I suggest that you instead use something like “Negative values denote net increase of soil C ….. and also suggests that the reference to the atmosphere  only is valid when considering the entire ecosystem, not just the soil system.

Answer18:  Agreed, we will rephrase the sentence as suggested.

L117  “The areas and proportions of FTYPEs of all drained peatland forests remaining forest in southern and northern Finland,”

           !Something is missing in phrase in italics above

Answer19: “Forests remaining forest” is a concept used in the greenhouse gas inventory to describe forests that did not undergo land use change. We will explain this.

L258  ??? “uncertainty less than 100 %;” what does this mean, 2% or 98% or what? Reformulate

Answer20: The expression was unclear, we will rephrase it. Also most of the Appendix tables (A2-A10) were accidentally dropped from the submission. Please see the missing tables in our AC’s to RC3. We use the IPCC (2006) Guidelines convention, where “uncertainty” means 1.96 x S.E.M. as percentage from the estimate. In this case the uncertainty of the whole country net estimate is 46% (last number in column “U, %”, Table A10). When the uncertainty is less than 100%, it means that zero is not included within the 95% confidence limits.

L256 – 264      would very much prefer to have data first presented related to unit area, e.g. ha and then as areal totals. Just having national or regional totals makes it impossible to relate to quantitative data from other sources.

Answer21: Agreed. We will add per unit area emissions where appropriate.

L296  give reference to “Yasso07 modelling”

Answer22: We will add the references Tuomi et al. (2009, 2011), already cited in methods on L144.

L 320-321       for the autotrophic CO2 sink strength you must include also the forest floor vegetation component. If not including you must at least do a sensitivity analysis on how not including that term affects the results.

Answer23: The litter production of ground vegetation as an input to soil is included, see L160.

L 330-331       the increase in annual temperature is NOT relevant. It is only changes in temperatures above zero (simplifying but much better than referring to annual averages) that actually affects the production or decomposition. If winter time temperatures are -10 or -4 does not affect either litter production or decomposition. Please refer to only seasonally relevant temperatures. Also differentiate between direct temperature effects and e.g. changes in growing season lengths.

Answer24: The original model that we use comes from Ojanen et al. (2010), where the relationship between CO2 measurements and the seasonal temperature (May-October) was established. We will modify the phrasing e.g. as follows: “The increase of 1.2 C in mean annual temperature across the time series, of both southern and northern Finland (Fig. 2) probably reflects the changes in conditions relevant to soil CO2 emissions, with an increase in CO2 emissions from soil by 8.1 Mt CO2 in the whole country…”. Yasso07 decomposition model is configured to use the annual temperature in calculations.

L 332 how can the temporal increase in soil CO2 flux be 8.1 when you in the result section state a change from 1.4 to 7.9 Mt over the studied time period?

Answer24: This value is the effect of increasing temperature when the BA and harvest remain at the level of year 1990. It is higher than the increase in the net soil CO2 balance because increasing BA and harvest rates counteract the temperature effect. This is explained on L332-335 and illustrated in Fig. 8.

RC2: 'Comment on egusphere-2022-1424'

This paper developed a new method to estimate soil CO₂ emissions based on empirical data and models for SOM decomposition and litter production from drained peatland forest in Finland. There are some merits for this study, which also provide new results can be utilized in IPCC.

Answer1: Thank you for the views that support the manuscript improvement.

However, I am not convinced by the predicted data at the current stage. The major concerns are lacking validation of the calculated soil CO₂ emissions.

Answer2: Please, see above our Answer2 to RC1.

The yearly time-scale is also not promising.

Answer3: Please, see below our Answer37.

Second, the authors claimed that water table depth is the main factor that controls decomposition in drained wetlands. So why not predicting water table depth and then calculate soil CO₂ emissions?

Answer4: New methods for estimating water table depth (WTD) in drained peatland forests are under development, including process modelling, but these methods are also challenged by difficulties to validate the estimates and to extend their results to the whole time series needed. Currently, the main source of forest data in Finland, the NFI, does not monitor WTD in drained peatland forests, but records several features that indirectly give information of peat moisture conditions. When WTD monitoring becomes realistic and the models can be reliably validated with sufficient coverage in different drained peatland forest site types, more appropriate models for soil CO2 balance can be employed. The model described here is as a crucial improvement to the approach earlier in use in the Finnish GHGI . The reasons why we could not use WTD as a predictor are explained in the manuscript on L443-450.

Some technical comments:

• The abstract is hard to understand at the current stage. The authors should improve it.

Answer5: Agreed. We will simplify and rewrite the abstract.

• Line (L) 13, explain the meaning of LULUCF.

Answer6: This abbreviation of Land Use, Land Use Change and Forestry will be dropped from the abstract. All necessary explanations of abbreviations will be given in the introduction.

• L30, explain GHGI.

Answer7: We will replace this by “GHG inventory” as elsewhere in the abstract.

• Lines 36-50, the logic of these two paragraphs are a bit of confusion. What do you want to say?

Answer8: With these two opening paragraphs we explain the reasons for our methodological work, describe and quantify the targeted land area and describe the importance of CO2 emissions and removals in drained peatlands for the Finnish GHG inventory. We will edit the paragraphs to clarify our message.

• 1, CO2 should be CO₂.

Answer9: The typo will be corrected.

• The space between value and % can be deleted.

Answer10: The spaces will be removed.

• What are the units of equations 1 and 2? What’s the difference between carbon balance and CO₂balance?

Answer11: The litter inputs to the soil system enter as biomass carbon, and the emissions from heterotrophic respiration exit as CO2. We will improve the description by adding units in the adjoining text.

• Figures and Tables should be shown in order.

Answer12: Agreed. We will check the order of images and tables.

• The authors used annual temperature, precipitation, and other climatic data to calculate soil CO₂That would cause large discrepancy between the calculated and actual data. I would suggest the authors calculate the daily data, at least monthly data.

Answer13: We agree that for CO2 fluxes short time scale dynamics matter a lot. However, our method is aimed at calculating annual emissions for GHG inventory purposes and the detailed work of linking CO2 emission rates to daily, and further, to annual temperatures was carried out in Ojanen et al. 2010 and Ojanen et al. 2014.

• “Old calculation method” is not a good name, which can be revised to the name of this method.

Answer14: We will consider renaming the old method.

• Results, how can you convince the readers if your data do not have any validation? 

Answer15: Please, see our AC1 Answer2 to RC1.

RC3: 'Comment on egusphere-2022-1424'

General comments

The manuscripts present a new way to estimate the CO₂ contribution from forested drained organic soils, to be used in national inventories for the reporting to UNFCCC. The method is dynamic and can take into account effects of climate change. This is highly needed as these ecosystems are a high source of emissions for a large number of countries.

The new method uses regressions equations based on a large number of investigations in north and south of Finland and from ecosystems with different fertility. The fertility as determined based on the ground vegetation, that also is monitored in the Finnish monitoring program, is used to estimate the different heterotrophic CO₂ flux. Also, the Basal Area is used in the regression equations to estimate input of C to the soil and as an indicator of the drainage status. Some of the components of the total estimates has been generated by using ecosystem model (Yasso07) as for example the amount of harvest residuals or stumps after harvesting.

The method shows that the Southern areas of forest on drained organic soils are net source of CO₂ although with high forest growth. The Northern sites is a sink but may become a source in the future, due to the “coming” temperature increase that is expected. The managing effect as harvesting and the forest residuals form this had a large effect on the net CO₂ budget.

The manuscript is a highly valuable contribution for to increase the use of the national inventories and gives a possibility to prognose future changes due to both management effects, but more so by a changing climate.

However, it needs a major revision.

Answer1: Thank you for noting the importance of the paper, and for the valuable suggestions to improve the manuscript.

I have not been able to conduct a detail review of the manuscript due to that tables A2 to A10 in the annex is missing. At least in the pdf documents that I could download from the egu website, but I assume that the conclusion is a presented in the discussion. Thus, most of the uncertainties is in the CO₂ temperature regressions as shown in Ojanen et al 2014.

Answer2: We apologize, the tables were accidentally dropped in conversion to preprint format. However, as suggested by the reviewer, the main message of the tables was explained in the discussion. The tables will naturally appear in the finalized manuscript, but we also present them here.

Table A2. NFI12 estimates of basal area of trees and their standard errors (s.e.) and relative standard errors (RSE) due to sampling assessed as explained in Korhonen et al. (2021, Supplementary file S1).

Table A3. Covariance matrix  of the parameters of peat and litter decomposition model derived from Ojanen et al. (2014, Table A.5) after combining the Mtkg and Ptkg subtypes.

Table A4. Covariance matrix  of the parameters of the ground vegetation litter model derived from Ojanen et al. (2014, Table A.4) after combining the Mtkg and Ptkg subtypes.

Table A5. Covariance matrix  of the parameters of the fine root biomass model of Ojanen et al. (2014, Table A.2).

Table A6. The applied variances of site-type specific fine-root turnover rates, Var() (expert judgment), and dwarf shrub coverages, Var() (Ojanen et al. 2014, Table A.3, after combining the Mtkg and Ptkg subtypes); the corresponding values  and  are given in Table 3.

Table A7. Relative standard errors (%) of litter production from living trees and from harvests and natural mortality on drained peatlands estimated from NFI11.

Table A8. Correlations of NFI estimates of litter production from living trees.

Table A9. Estimates of CO₂ release from peat and litter decomposition, net C inputs to soil converted to the units of CO₂, and soil balance CO₂ balance (“Net”) for year 2021 together with the variance (“Var”) and uncertainty (“U”) of the estimates.

Table A10. Estimates of change from 1990 to 2021 in CO₂ release from peat and litter decomposition, net C inputs to soil converted to the units of CO₂, and soil balance CO₂ balance (“Net”) for year 2021 together with the variance (“Var”) and uncertainty (“U”) of the change estimates.

The material is highly complex, with a lot of abbreviation (not all explained as GHGI line 30), referring to regressions (manly in Ojanen et al 2014) and Yasso07 modelling results, so that the concepts used – that I believe is correct, is unclear and hidden.

The abstract is hard to understand, has to be redone.

Answer3: We agree. We will produce a diagram of the different steps of the method to help the reader to follow the calculation. Also, we will simplify and revise the abstract. The abbreviation GHGI will be removed and called GHG inventory in the edited manuscript.

It is comparing the new method with the “old“ used in Finland and the IPCC default method, this needs to be better described. Is the “old method” published more than in the reporting documents for the national reporting? If the old method is not “published” it has to be presented in the supplement, as the reader needs to be able to compare the underlaying assumptions for the two methods.

Answer4: The old method has not been published as a full paper, but we agree, the reader needs to know the main differences between the old and new method. For this purpose, we describe the main assumptions of the old calculation method on L244-253. We will check if we can further elaborate this text.

The underlaying concepts of the new method is not clearly presented. For example, that al autotrophic fluxes are deleted. My suggestion is that one makes a first figure were the different compartments of the CO₂, and pools used in the different methods are presented. This should also include the IPCC default method – as the new one also use the C flux from the discharge (stream, lakes etc) from the default one.

Answer5: Good point, we will compile a diagram of the different compartments and pools and the links connecting these for the new method.

One of these concepts (assumptions) that are not presented in the manuscript, but is there, is that it will not be any change in ground vegetation biomass over time. The changes from the ground biomass is taken into the method, in detail both by above and below litter input to the soil and its effect on heterotrophic soil CO₂ emission. The effect of the input from the ground biomass in the low fertile system, is shown by a “moss” driven soil organic matter growth. – I agree on that the ground vegetation biomass can be assumed to be constant during most of the stand rotation. But is this the case after harvesting on the fertile system? There will be a bush/shrub increase that will compensate partly for the organic decomposition, that will be emitted during the first thinning. – I presume that no data is available on this at a national scale, but this aught to be simulated using the Yasson07 model. – You need to argue for that the ground vegetation can be assumed to be in a steady state, this is missing.

Answer6: True, dwarf shrub areal cover is assumed to remain static for different FTYPEs (Table 3), but the regression models (Table 4) that predict arboreal fine root biomass (which in turn is used to predict arboreal fine root litter input) have BAs of trees as predictors and can thus follow changes in BA. For ground vegetation litter production (excluding the dwarf shrub belowground litter), the models (Table 5) make use of the BA - litter production relationship of herbs and mosses (Ojanen et al. 2014), thereby leading to changes also in ground vegetation litter production following changes in BA. We will elaborate this aspect in the revised manuscript. Overall though, we agree that short-term harvesting disturbance on ground vegetation (either negative or positive) is not explicitly implemented in the present model. This deficiency is discussed with other strengths and vulnerabilities of the method on L459-469.

The overall concept and work holds for the new method, but is not presented as well as you could!

Answer7: We hope the diagram that we will compile of the calculation steps will improve the presentation of this rather complicated method.

Nearly all table and figure legends need to be redone. All needed information in understanding a figure should be in the text, not referring to other tables. Thus, the abbreviations for the site fertility have to be presented, with the information on how this is related to site fertility.

Answer8: We agree. The captions will be completed as suggested.

Detailed comments

Line 129 the reference is FAO 2018, but the text in the reff is from 2020?

Answer9: The reference will be corrected to 2020.

Line 179 to 185. The minirhizotron section. Here the effect of “stabilization” after the installation, needs to be discussed as it takes 4 years to have a steady state (Strand et al. 2008 Science). Furthermore, there are no uncertainty values for the determined root turnover rates in Table 3.

Answer10:  We measured fine root longevity during four years, after one year stabilisation time after the installation of the tubes. It has been stated that minirhizotrons underestimate longevity during short (<3 year) studies (Strand et al. 2008) since the stabilization after installation may take several years. The study sites in Strand et al. 2008 were all on mineral soils and the tubes were installed in position of 45 degrees into the soil. Such an installation requires heavy digging of soil, cutting the roots from a wide area and causing heavy disturbance to the soil ecosystem. In our case, the tubes were installed to peat soil by making a small hole to the peat with a pointed stick and pushing the tube down to the soil. No digging of soil took place. Thus we believe that the disturbance to the soil was actually very small, and one year stabilisation time was enough to start the measurements.

The results are preliminary and the uncertainty values have not been determined yet.

Table 2 What are the units?

Answer11: There are no units as the values represent rates, i.e. the proportion of the component mass that turns into litter in a year. This is explained on L170-171, but we will also add the explanation to the table title.

Line 258  .. (uncertainty less than 100% ; Table A 10 in Appendix).. Table missing and what do you mean?

Answer12: The expression was unclear, we will rephrase it. Also most of the Appendix tables (A2-A10) were accidentally dropped from the submission. Please see the missing tables above. We use the IPCC (2006) Guidelines convention, where “uncertainty” means 1.96 x S.E.M. as percentage from the estimate. In this case the uncertainty of the whole country net estimate is 46% (last number in column “U, %” in Table A10). When the uncertainty is less than 100%, it means that zero is not included within the 95% confidence limits.

Line 272 .. northern and south Finland .. please help the reader by always presenting the data as south  in comparison with northern, as mostly done in the manuscript.

Answer13: OK, we will keep the order the same throughout the manuscript.

Line 397 .. (and other climate variables in Yasso07).., what variables? And should not the parameters used in the model be presented in a supplement.

Answer14: We assume this comment is targeted to L297. These variables are explained on L222 and shown in Fig. 3 and Supplementary Fig. 2.

Line 425 IPCC 2014 missing in the reference list, should it be 2013?

Answer15: The IPCC 2013 Wetlands Supplement was published in 2014 as listed in References. 2013 is part of the name of the document.