the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 27 Jul 2026
Linking moss cover, soil organic matter fractions, and carbon stabilization pathways in temperate forest ecosystems
Abstract. Moss cover is increasingly recognized as a biotic driver of soil organic carbon (SOC) dynamics in forest ecosystems, yet its influence on C stabilization across functionally distinct soil organic matter (SOM) fractions remains poorly quantified. How moss cover interacts with forest type and parent material to regulate C partitioning into mineral-associated organic matter (MAOM), the most persistent SOC fraction, is largely unknown in temperate forests. To address this gap, we investigated SOC distribution among free particulate organic matter (fPOM), occluded POM (oPOM), and MAOM across moss-covered and no moss soils in two contrasting temperate forest types differing in parent material. A total of 42 topsoil samples (0–2 cm) were collected from a coniferous mixed forest on sandstone and loess parent materials (Baden-Württemberg) and a pine forest on sandy parent material (Brandenburg). Physical density fractionation was applied to resolve SOM fraction distribution, and total nitrogen (TN) and C:N ratios were determined alongside carbon stabilization efficiency (CSE), calculated as mineral-associated organic matter carbon (MAOM-C) / SOC × 100, as an integrative index of stabilization capacity.
Moss-covered soils showed significantly higher SOC and TN concentrations than no moss soils, with the strongest effects observed in the coniferous mixed forest on sandstone parent material and negligible in loess. MAOM-C concentrations significantly increased under moss cover in the coniferous mixed–sandstone environment where CSE nearly doubled compared to no moss soils. Biotic factors, in particular the interaction between moss cover and forest type, were the primary predictors of stable C, while parent material exerted no independent effect. These results demonstrate that moss cover is linked to distinct C stabilization pathways, favoring mineral-associated stabilization in coniferous mixed forests and accumulation of labile C fractions in pine forests, underscoring the importance of incorporating moss cover as a biotic driver in SOC models and temperate forest C accounting frameworks.
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Status: final response (author comments only)
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RC1: 'Comment on egusphere-2026-4029', Anonymous Referee #1, 29 Aug 2026
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AC1: 'Reply on RC1', Madhavi Parajuli, 10 Sep 2026
Dear Reviewer 1,
Thank you for your thoughtful and constructive comments.
We sincerely appreciate the time and effort you invested in reviewing our manuscript and the valuable points you have raised regarding the terminology, presentation of results, statistical interpretation, and discussion of SOC stabilization pathways.
We have carefully considered all of your comments and will revise the manuscript accordingly. In particular, we will clarify the terminology used throughout the manuscript to distinguish between physically separated SOM fractions (fPOM, oPOM and MAOM) and the organic carbon (C) concentrations or proportions associated with these fractions. We will also revise the label and caption of Figure 3. In this regard, we would like to clarify that the values presented in Figure 3 represent the mass proportions (%) of the physically separated SOM fractions obtained through density fractionation rather than the relative C concentrations within these fractions. Furthermore, we will refine the description of the relationships among labile and mineral-associated C pools and reconsider the statements that may imply direct C transfer or specific mechanisms that are not directly demonstrated by our data.
We will address all the provided comments point-by-point, and the corresponding changes will be incorporated into the revised manuscript. We greatly appreciate your constructive feedback, which will help us to improve the clarity, scientific rigour and, as a whole, the quality of our manuscript.
Kind regards,
The authors
Citation: https://doi.org/10.5194/egusphere-2026-4029-AC1
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AC1: 'Reply on RC1', Madhavi Parajuli, 10 Sep 2026
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RC2: 'Comment on egusphere-2026-4029', Anonymous Referee #2, 31 Aug 2026
Dear Editor,
These are my comments about the paper 'Linking moss cover, soil organic matter fractions, and carbon stabilization pathways in temperate forest ecosystems', from M. Parajuli et al., submitted for publication to EGUSPHERE.
GENERAL COMMENT
The experimental work is well performed; I did not see any detail to be seriously discussed. The main core of the paper, the density fractionation procedure, is described with enough detail (an experienced laboratory worker may reproduce it without too much problem).
That said, the experimental work is limited. Authors performed a density fractionation to obtain fPOM, oPOM and MAOM (which is good), but nothing more (or very little more). There is not a characterization of these fractions (not even a basic characterization such a acid hydrolysis), nor further characterisations of SOM that could add more and relevant information. This limits seriously the possibilities of understanding or interpreting the results obtained for fPOM, oPOM and MAOM. We do not know whether fPOM is more biochemically recalcitrant than MAOM, nor we have a minimum of information about the composition of the obtained fractions. Most particularly, because many of the studied samples may have been seriously affected by mosses, whose biochemical composition has been much less studied than forest litter. In the samples under forest litter we may make assumptions about the composition of fPOM, oPOM or MAOM, by taking as a reference other papers in the literature about SOM in forest soils. But I do not dare to make assumptions about how mosses may have changed the composition of these fractions.
It is also relevant the scarce characterization of the mineral component of the studied samples. Their textures, for instance, are not given, only loosely mentioned (without quantitative data) in the description of the sites. There is no data about the abundance of Fe or Al oxyhydroxides. Soil texture --more specifically, the abundance of fine silt and clay -- and the abundance of iron and aluminium free forms are determinant for the capacity of soils to stabilize organic matter as MAOM; therefore the lack of this information makes very difficult to propose an explanation about why MAOM is more abundant in one place than in another one.
Sometimes I had the impression that authors try to stretch the data in order to increase (somewhat artificially) the length of the article. At some point the presentation of the results becomes a bit repetitive. This is achieved by increasing the number of statistical tests beyond what is reasonable. In my opinion, the results obtained are sufficiently well presented in figures 2-6. Figure 3 is actually redundant with table 1: they give the same information. I propose to eliminate figure 3 because, in fact, it gives less information than table 1. Figure 5 and table 3 are also redundant: the figures do not give the significance of the regression lines represented, but this is easily solved by adding the 'p' value after R2 (example: R2 = 0.512, p = 0.043), or the appropriate asterisks (ns, *, **, etc). I propose, in short, to eliminate redundancies that give a somewhat bad impression, as if the authors wanted to make the article longer than necessary.
Besides this problem of an unnecessary length of the paper, the lack of this complementary information (you have fPOM, oPOM and MAOM, nothing more) results in a difficulty to explain your results. Authors can establish the effect of moss cover on the results, the effect of vegetation cover, and the interaction between these two factors, and not much more than this. The effect of parent material can be added, but since the 'vegetation' and the 'parent material' factors are nested, care is needed when looking for its effect.
An important statement is given by authors in lines 423-424: 'The underlying research data are not publicly available because they form part of an ongoing research project but may be made available by the corresponding author upon reasonable request'. Which is ok, but it is also the recognition that this work is in some way an advance of a more extensive work currently underway. This probably explains the relative shortness of the dataset that underlies the current paper. All this has an important consequence: there is little basis for a long discussion. In the article, the discussion spans almost 4 full pages, and is in great part speculative. In my view it could be shortened to 2 ot 2 1/2.
Essentially, in my opinion the paper should evolve in one of these two ways:
1) Shortening the paper, by reducing unnecessary repetitions and focusing on the obtained results. Avoid results overinterpretation: remember the lack of auxiliary data that could help to explain your results. The result should be a shorter, more focused paper. Or
2) Extend the dataset. Give data about the mineral component of the soil samples, specifically soil texture (fine silt and clay contents) and Fe/Al oxyhydroxides. I would expect that these data should be crucial to explain MAOM accumulation, including the possibility to obtain a predictive model for MAOM accumulation. If you could add also some biochemical characterization of the obtained fractions (e.g., acid hydrolysis), the result could be a really impressive paper.
I would prefer the second option, to be honest. But I suppose that the first one will be the chosen option. Either one will be acceptable to me.
SPECIFIC COMMENTS
Lines 55-56. I disagree with this way of simplifying what happens in a soil. According to these two lines, the sequestration capacity of soils depends only on the amount and characteristics of organic inputs, with little or no role of the mineral matrix. Later in the paragraph authors mention the association to minerals as a vector of SOM stability (lines 57-58), meaning they are well aware about these constraints. Please try to put this in a better organized way. The role of the mineral matrix must be mentioned from the beginning: actually, is the main constraint for SOM stabilization.
Lines 65-66. These lines are somewhat redundant; essentially you say that SOM fractionation is essential to understand SOC fractions, which is somewhat a circular argument. Try to improve writing.
Line 133. Specify the method used for analysis of total C and N, I assume an elemental analyzer (based on Dumas' method): ThermoQuest, Perkin Elmer, LECO or similar, but mention it anyway. I assume that soils were carbonate-free, and therefore total C = organic C: if so, please mention it.
Figure 2 (lines 173-174). I am very surprised by the results of the ANOVAs, specifically about the significance of the factors (forest type, moss cover Y/N) and the interaction between them. In the figures for SOC and total N, no problem with the high significance (p < 0.001) of the forest type: it is obvious. I am more surprised by the non-significance of the moss cover. But particularly, I am surprised by the non-significance of the interaction between them. The lack of interaction should mean that the behaviour of the factor ii (moss cover) is about the same at both forest types: and this is not what happens. In coniferous mixed forests, SOC concentration is higher under moss cover, whereas in pine forest is lower. Same with total N. Thus I would expect significance for both forest type, moss cover, and interaction between them. Revise the ANOVAs results, please.
Page 8. Both figure 3 and Table 1 are good. But they refer to the same set of results. Thus they are redundant. In my first years as researcher I learned that results must be given either as a figure, or as a Table, but not both at the same time. The figure is nice, but actually Table 1 gives more information.
Figure 6 (page 12). Consider seriously homogeneizing the scale of the Y-axis in the three sub-figures. This could add a relevant information to the reader, which is to show that the values of the Carbon Stabilization Efficiency are notably diferent between sites. Besides the effect of moss cover, no doubt there is a great effect of soil texture (abundance of fine silt plus clay) and soil mineralogy (presence of iron oxihydroxides, aluminium, exchangeable calcium).
Lines 155 to 163. How this analysis has been done is not obvious, and the paragraph 2.4 is not explicit enough. In a multiple linear regression we try to fit an equation of the type y = b0 + (b1 * x1) + (b2 * x2) + ... + (bn * xn), where 'y' is the numerical result we want to explain (in your case, the amount or proportion of MAOM), x1 ... xn are the numerical values (experimentally obtained) of the 'n' variables that should explain 'y', and b1 ... bn the coefficients for each of these 'n' variables. The problem is that in multiple linear regression all values in the right half of the equation are numeric (both 'b' and 'x' values), whereas in your model the several components ('x' values) of the model to fit are factors (y/n). How did you calculate the model given in Figure 7? Did you replace these factors (x1 ... xn) by numeric values (1/0)? Or rather did you actually apply a multivariate analysis, which is not exactly the same as a multiple linear regression? [I have seen often problems with the precise denomination of statistical tests, which may have different names depending on country: USA, Italy, France...]. At any rate, please give a bit more of detail about how this analysis was done, in order to understand well Figure 7.
Lines 271-273. I have serious difficulties to take seriously the non-effect of parent material on MAOM. As I mentioned in my previous comment, soil texture (abundance of fine silt and clay, clay type), exchangeable calcium and Fe/Al oxyhydroxides are crucial to generate MAOM, and these properties are largely determined by the soil parent material. I am skeptic about the statistical analysis presented in Figure 7. Apparently the 'parent material' factor has not been studied altogether, since 'sand' and 'loess' have each one its own 'beta' value. Same happens with the 'moss cover' factor, which apparently has been split: what is the difference between the 'Moss cover' factor and the 'Moss effect in pine forest'? According to the figure foot (lines 275 and following) the figure represent a multiple linear regression model, whereas the several predictors (moss cover, parent material, vegetation type) are not quantitative but qualitative (Y/N for the moss cover, sand/loess, pine/mixed forest).
Lines 284-286. 'The interaction between moss cover and pine forest was the strongest...' and 'the stabilizing effect of moss on SOC depends on forest type' are the obvious conclusions that arose from the mere visual inspection of figure 2 (page 7), which actually is very clear (and I congratulate authors for it). However, this is in gross contradiction with the non-signification of the interaction between 'Forest Type' and 'Moss Cover' stated in Figure 2. How does it all fit together? To me, there must be an error in Figure 2. Verify, please.
Lines 334-336. Replace 'microbial-derived compounds' with 'organic', simply. Another possibility is to say 'organic compounds, mostly plant-derived, more or less micorbially reworked', or something similar. The binding of organic compounds to mineral surfaces, through a variety of possible bonds, is the main path to generate persistent SOM. But this 'persistent SOM' may come from microbially-transformed organic matter or from relatively fresh organic matter. Assuming that microbial-derived compounds are the only source of stable SOM is extremely debatable, and is an assumption with which I disagree.
Citation: https://doi.org/10.5194/egusphere-2026-4029-RC2 -
AC2: 'Reply on RC2', Madhavi Parajuli, 10 Sep 2026
Dear Reviewer 2,
Thank you for your careful, constructive and insightful comments.
We sincerely appreciate the time and effort you invested in reviewing our manuscript and the valuable suggestions you have provided regarding the scope of the dataset, redundancy elimination, manuscript length and interpretation of the results.
We have carefully acknowledged all of your comments and agree that additional data, particularly of Fe and Al oxyhydroxides, fine silt and clay contents, would provide valuable complementary information to further understand the mechanisms underlying SOC stabilization. We consider these measurements important for future work and intend to incorporate such analyses in subsequent research. For this present manuscript, we have chosen Option 1, as suggested, and will therefore focus on shortening the manuscript, removing unnecessary redundancies, avoiding overinterpretation, and ensuring that the discussion remains closely aligned with the results directly supported by our data. We will also carefully re-examine the ANOVA results and statistical analyses and clarify their presentation and interpretation where necessary.
We will address all of your comments point-by-point, and the corresponding revisions will be incorporated into the revised manuscript. We are very grateful for your constructive and thoughtful feedback, which will help in improving the clarity, scientific rigor, focus, and overall quality of the manuscript.
Kind regards,
The authors
Citation: https://doi.org/10.5194/egusphere-2026-4029-AC2
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AC2: 'Reply on RC2', Madhavi Parajuli, 10 Sep 2026
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Summery
This paper reports on a statistical analysis of 42 German topsoil samples collected from two forest types situated on one to two parent materials, with and without moss cover. The study examined soil organic carbon (SOC) contents and its fractions including free and occluded particulate organic carbon (fPOC and oPOC), as well as mineral-associated organic carbon (MAOC). Overall, it was found that moss cover was associated with higher MAOC contents.
General Comment
This is a well-written and well-designed study that would benefit from several clarifications (see below).
Specific Comments
L34: What does "disproportionally" refer to in this context? The term needs clarification.
L69-70: “While most studies…” - please provide references to support this statement.
L76: The hypothesis regarding C:N ratios appears without prior justification. Please provide rationale earlier in the introduction to establish the basis for this hypothesis.
L170: I believe the mixed conifer forest is located “near” Tübingen rather than “in” Tübingen. Please check this geographical description.
Figure 3: The x-axis should be labelled "SOC fractions" rather than "POM fractions." l believe, organic carbon - not organic matter - was determined; this should be clarified throughout the manuscript.
Table 1: This table is redundant with Figure 3 as it presents overlapping information. Consider a consolidation.
Table 3: For the mixed conifer forest with moss cover under loess, MAOC increased as the labile organic carbon pools (fPOC + oPOC) decreased. To me, this suggests a potential redistribution between pools for these sites – as a transfer from labile to more stable pools due to other faction (e.g. moss species or microbial community). Perhaps, fine-textured soils have sufficient mineral surface area to bind additional OC inputs from the POC pool, promoted by mosses. In contrast, soils under sandstone do not appear to have the capacity for such redistribution as slope is positive. Just think about my interpretation of your data.
Figure 7: Regarding parent material (sand): since the effect was not estimated, this could be omitted in figure.
L317-18: The phrase "..slower decomposition … N-limitation" would logically lead to increased carbon storage. Please clarify the intended meaning.
L320: "Stabilization dominated SOC fraction…" - This sentence is unclear and may be reworded .
L352-53: “These results… sandstone environments”. I would interpret this differently: labile POC increases alongside MAOC pools , suggesting no active redistribution (i.e., “movement of POM into persistent pools”), but rather that both pools increase simultaneously with specific site conditions.