the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
Afforestation induced shift in the microbial community explains enhanced decomposition of subsoil organic matter
Abstract. Afforestation on former pastures is widely promoted due to its potential to increase soil organic carbon sequestration while reducing CO2 emission. The establishment of a forest on a former pasture, however, might affect soil microbial community structure due to the alteration in substrate quality and thus impact carbon cycling in soils. To date, it still remains an open question if and how afforestation may alter the soil microbial community structure and related implications for soil organic matter stabilization. In addition, the majority of studies focuses on low altitude regions which results in uncertainties regarding the effects of afforestation on soil microbiology in mountainous regions. In this study, we aimed to investigate the consequences of afforestation of a subalpine pasture with Norway spruce (Picea abies L.) on the soil microbial community structure following 130 years of afforestation. We used a multi-proxy biomarker approach, including phospholipid fatty acids (PLFAs) and glycerol dialkyl glycerol tetraethers (GDGTs), to explore the shift in the microbial community structure following afforestation with increasing forest stand age. We found a significant increase in bacterial communities (Gram- and Gram+ bacteria) with increasing forest stand age compared to the pasture. This trend, however, was reversed with increasing forest age when considering GDGT biomarkers. We thereby conclude that the microbial community in the pasture and forests of different forest stand ages utilize different carbon substrates as food resource, which is a direct consequence of the modification in litter input after the conversion of a pasture to forests. Our data further suggests that an increase in the soil organic matter decomposition results from the alteration in the microbial community structure, which is especially evident in the subsoil of the 130-year-old forest stand ages.
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RC1: 'Comment on egusphere-2024-870', Anonymous Referee #1, 04 Jul 2024
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Review for “Afforestation induced shift in the microbial community explains enhanced decomposition of subsoil organic matter”, egusphere-2024-870 by Tatjana C. Speckert, Arnaud Huguet and Guido L.B. Wiesenberg submitted to Biogeosciences.
General comments
The authors use two proxies, PLFAs and GDGTs, to study microbial community composition along a well-characterized forest stand age gradient (land use change from pasture to forest). The manuscript is well written and presents solid data from an interesting study. Most formal criteria in terms of data quality, presentation, statistical evaluation, etc. are met, and all results are presented in an objective way. However, I get the impression that the paper in its recent form confirms what we already knew.
For example, “enhanced decomposition” is in the title, but I can’t see where this is discussed or shown by the authors for these samples. On the other hand, the obvious disagreement between the two proxies is not discussed at all, although this would be the major surprising result. As the authors point out themselves, this might be related to the differences in turnover times of the chosen markers (PLFAs reflect more recent microbial community, GDGTs longer-term community); it would be very interesting to deepen the discussion in that regard. The authors discuss the effect of seasonality but do not discuss the sensitivity of PLFAs and GDGTs to seasonal differences (e.g., [1], or from their own experience). The authors also miss that the studied afforestation sequence may be unique (especially looking at the weak age gradients due to the seemingly “outlying” 55-year old site) and hence miss pointing out that one should study this effect not only using one gradient in future research.
Looking at the paper as a whole, I suggest major revisions. The scope needs to be sharpened and the data need to be presented in a way that answers questions related to clear hypotheses which are not obvious now, besides that vegetation shift equals soil microbiome shift; if the paper is about enhanced decomposition and subsoil, there should be hypotheses related to these processes, or soil horizons. Figures should help to answer the questions related to the hypotheses and not merely present all data in an albeit objective, yet undirected way (“story missing”).
Yours sincerely
Specific comments
- Title seems misleading. Enhanced decomposition of subsoil organic matter is not discussed
- Line 31-44: This framing somehow is misleading as your own data show that there is no SOC sequestration effect; maybe base this section more on the surprising finding of no increased SOC stocks despite 130 years of afforestation in your prior paper, and how SOM quality and lability might still be different
- Line 82: Entering “GDGTs PLFAs” in Google Scholar, I find ~190 results and already among the first five is a study from mountain sites [2] which seems to be excluded because it does not explicitly deal with afforestation gradients; I plead the authors to widen their focus to discuss their data, especially to check whether other authors have found a similar mismatch in total PLFA and GDGT yields
- Lines 91 and after: This section is very confusing as it mixes up labile/ recalcitrant/ pasture/ aged forest stands; I’m also not sure whether the sole evidence of higher C/N ratios justifies the assumption of a higher “recalcitrance”; this should be backed up by short-term incubations or sth. alike. The paragraph should end strong and with clear messages as its purpose is to clearly explain the outset of the manuscript
- Line 168: I do not really see how the GDGT indices help the study. It would make more sense in my view to use the sum of all PLFAs and GDGTs to contrast the patterns observed in their total yields across the gradient and depths; both are proxies of microbial bio/necromass and could help to sort out source contributions to SOM; not sure how pH or temperature-correlated indices help e.g., in line 352 – 358, besides providing reference values to compare with other studies (which may be more relevant to ensure quality of the data?). In short, I would put much more focus on the apparent mismatch between markers of microbial bio/necromass and what could explain this. Some starters are already brought up in the discussion, but this should be deepened (see also point 7).
- Line 287-291: Please deepen this section more. Try to provide some estimate how sensitive PLFAs and GDGTs could be to seasonal variation from others [1] or your own experience, or at least point out that this should be tested in future.
- Conclusions: Disagreement between PLFAs and GDGTs is not mentioned at all. What is the specific community shift that you mean? And how can you be sure that this is solely explained through the changed litter input if you cannot even rule out seasonality effects and state yourself that GDGTs and PLFAs might represent completely different community dynamics based on their turnover? The statements on the link between microbiome shift and SOM decomposability/ quality seem far-fetched to me given what the authors have presented in the MS. Instead of longer afforestation sequences as suggested in line 434, I would rather advise to increase the number of afforestation gradients from 1 to at least 3 in different geologic/ climatic settings, and discuss the uniqueness of the site and why the 55-yr forest stand obviously disagrees with linear changes with forest stand age. It could also be discussed whether today’s pasture is an appropriate “control” as it does not represent the state of the pasture 130 years ago.
- “Subsoil” is not even mentioned in the conclusions despite it being mentioned prominently in the title. Revise the paper accordingly.
Technical corrections
Abstract
Line 24 How was it reversed? Be more specific
Line 25-28 These statements seem unjustified by the information that you provide in the abstract, provide more justification
Introduction
Line 40 “plays” à “play”
Line 41- 44 “potentially”. As this seems to be a central assumption of the paper it would be good to repeat some of the findings that lead to this statement and how it could be tested (and will be tested here, although I must say that I didn’t get the impression that this was shown, see my general points before).
Line 46-48 Link unclear, be more specific why one controls the other
Line 63 Why “even though”?
Line 66 “possibly feeding” – GDGTs do not feed root C. Please use correct wording. This also appears in other places in the MS (Line 347)
Line 82 To the best to our à To the best of our
Line 94 “to the pasture where less easily” this contradicts your prior statement that older sites have a more recalcitrant OM.
Line 96 “with increasing forest stand ages due to the more easily” again, this contradicts with what you stated earlier à clarify what sources of OM you consider easily/ hardly degradable and why (back up with literature), and how this affects allover SOM lability/ stability along afforestation and depth gradients
Methods
Line 113 How much grams of soil were used? how much absolute volume of solvents were used? When were the extractions performed if samples were taken already in 07/2020?
Line 120 The degree of detail for the LC gradient description is much lower than for the GC in the next section. Please provide more method details.
Line 129 How much absolute volume was used?
Line 136, 139 “Was done” à please rephrase.
Line 153 Please explain why p<0.95 is appropriate as a p-level for a Tukey HSD test
Line 154 How can one perform an analysis with one (n=1) replicate? This means to me, there were no replicates.
Line 162 standardized how? Mean=0, SD=+/- 1?
Results
In general, the results section was very heavy to read. Lots of information (good because: objective, but hard to follow because: unfiltered, no story apparent; no obvious finding that jumps at the reader). It might be helpful to generalize the results a bit more (e.g., contrasting total yields of PLFAs vs GDGTs along the sequence as indication of changed turnover of SOM, i.e., fresh biomass vs. older biomass/ necromass, and shifted community composition?). I also cannot see how the sections 4.1 – 4.4 are related to any scientific hypothesis brought up in the introduction (For example: 1 Resolving depth effects. 2 Resolving age effects. 3 Resolving combined depth/ age effect, i.e., decomposition degree effect.)
Discussion
Line 334 AFM à AMF
Line 334 “due” seems misplaced, sentence reads wrong
Line 355 Delete “range value”
Line 380ff Maybe this could be due to fewer but larger roots, i.e., less “homogenous” root system in forests?
Figures
In the results, there is a lot of mentioning of significance tests, but these are not reflected in the figures. Maybe asterisks or letters could be added to indicate significant correlations/ differences (this applies to Fig 02, Fig 05, and all Fig S1-S9)
Fig 03 Please add “depth” as a variable or color the dots according to depth
Fig 07 Same as Fig 03
Fig S1-S9 Think about using symbols for depth and colors for sites; the way it is used now, one is not necessary. Add significance levels to the r values. Only discuss significant correlations in the results
Refs cited
[1] https://www.sciencedirect.com/science/article/pii/S0038071712003252
[2] https://academic.oup.com/ismej/article/14/4/931/7474800
Citation: https://doi.org/10.5194/egusphere-2024-870-RC1 -
RC2: 'Comment on egusphere-2024-870', Anonymous Referee #2, 15 Jul 2024
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This manuscript reports on an observational and comparative study of soil microbial groups in grassland and forested soils of different ages. This topic in not without interest and aspects of the research conducted in this study have potential to interest the scientific community. However, the technique chosen to assess the microbial diversity is limited and not the most adequate one for this kind of study. The reason of choosing these methods should be addressed and the limitation of these methods compared to other which are largely used discussed. The manuscript would also improve with a deeper analysis of the data and a clearer discussion, better linked to the hypotheses.
Title: the title of this paper is misleading as decomposition is not assessed. I suggest adapting the title so it describes better the output of the study.
Introduction: The use of PLFA to study the biodiversity and abundance of prokaryotes and fungi in soils is limited from my point of view. It would be essential to explain in the introduction the advantage of using this technique over the nowadays largely used molecular methods such as eDNA metabarcoding (amplicon sequencing) or group specific qPCRs assays to assess microbial diversity and abundance in soils. Similarly, it would be necessary to state why it was useful and judicious to use GDGTs to study archaea and bacteria instead of molecular method such as eDNA metabarcoding or metagenomics. Archaea are relatively rare and not dominant in grassland and forest soils, usually accounting for less than 10% of the prokaryotic community. Why was it important to study them in that study?
Lines 74-78: Fungi are microbes! The expression “soil microbial and fungal communities” is misleading.
Hypotheses: The rationale behind the two hypotheses is not well described in the introduction. Moreover, the second hypothesis is confusing and would need to be rephrased. Also, some additional hypotheses could be formulated. For example: What would be expected according to soil depth? What would be expected regarding the ecology of the fungi assessed (saprotrophic versus mycorrhiza)? …
Methods:
Why were samples collected from 5 soil pits in the pasture whereas only 3 soil pits were used for each forest site? The reason for this unbalanced experimental design needs to be addressed.
In the data analysis: were the n=2 for PLFA and n=1 for GDGT technical replicates? Or these were true replicates? This is not clearly described. Also, the description of the number of data point is confusing (line 160-164). Why are each forest age have a different number of data points?
Paragraph 3.2: please describe the structure for the roman numbers and the letters (a, b, c) for the equations (could also be included in supplementary material).
Results: The data collected could be further explored and analysed according to the hypotheses. For example, the ordination plot presented in figures 3 and 7 would be more informative in my sense if all data points (from pasture and 40, 55 and 130 yo forests) would be presented in a same ordination plot, for a direct comparison of the “community” of the PLFA in the different sites. Then, the correlation with the soil properties and compounds would be done across the different soil and it would potentially become clear which compounds or soil properties would correlate to which soil type.
Discussion: The discussion is rather long and difficult to follow. It would merit a complete re-structuration. I would suggest structuring the discussion according to a newly formulated set of hypotheses. Then the discussion could be more focussed and easier to follow for the reader. For example, a large part of the discussion is discussed the pasture and the forest soils separately (paragraphs 5.1 and 5.2), whereas the goal of the paper is to compare these types of soils.
Some paragraphs of the discussion also do not place the findings into a larger ecological context, such as in the 2nd and 4th paragraphs of the discussion, which essentially try to explain why certain type of GDGTs are more prominent in certain soils but does not address what it would potentially mean for the functioning of the ecosystems, especially when comparing pasture and forest of different ages.
On the other hand, in some parts, the discussion is quite speculative, and several argumentations should be moderated. For example: “The change in the soil microbial community following afforestation on a subalpine pasture is a direct consequence of the alteration in organic matter input…” (line 414). This statement should be put in the context of the limitation of the available data in that study, in which “only” microbial groups with similar traits (G+, G-, etc) or different ecology (saprotrophs, AMF) were assessed and not the entire microbial diversity, and only C and N were measured in the organic matter (or did I miss something?).
Citation: https://doi.org/10.5194/egusphere-2024-870-RC2 -
RC3: 'Comment on egusphere-2024-870', Anonymous Referee #3, 26 Jul 2024
reply
This paper investigates changes in soil microbial communities during afforestation using a space-for-time approach ranging from pastures to a 130-year-old coniferous forest. The authors investigated microbial phospholipid fatty acids (PLFAs) and glycerol dialkyl glycerol tetraethers (GDGTs) in each vegetation type and to a depth of 45 cm in 5 cm increments (0-5 cm, 5-10 cm etc.). PLFAs allow for the quantification of microbial biomass of fungal (arbuscular mycorrhizal fungi and saprotrophic fungi) and bacterial groups (gram+ and gram- bacteria), while GDGTs allow for the quantification of archaeal (isoprenoid GDGTs) and a yet poorly described bacterial group most likely part of the phylum acidobacteria (brGDGTs).
The authors do a good job of explaining the importance of the topic and its relevance for global carbon sequestration.Title
It is advisable to change the title to better fit the results of the study. Currently, the title is misleading since decomposition rates are not estimated. Subsoils are mentioned in the title and partially in the discussion but are not really emphasized nor mentioned at all in the conclusion.
Abstract
The topic and its significance in the global context are well explained and highlight its novelty (focusing on alpine pastures) compared to similar studies.
The findings are presented well, however are not necessarily backed up by data and are therefore potentially misleading. For example, the sentence “Our data further suggests that an increase in soil organic matter decomposition results from the alteration in the microbial community structure, which is especially evident in the subsoil of the 130-year-old forest stand ages.” suggests the authors measured in situ decomposition rates of plant litter, which is not the case.Introduction
The introduction must state the current state of literature more concisely in regard to microbial communities and how they are shaped by their environment and vice versa in context of this study (pastures vs. coniferous forests).
The role of GDGTs has to be explained in more detail.- Only the core GDGT abundance is measured in this study. Conversely, the measured values correspond to the necromass of archaea (isoGDGTs) or (acido)bacteria (brGDGTs). It seems though as the authors interpret the measured values as microbial biomass. If this is the case this needs to be changed or addressed how you can use the coreGDGTs as an indicator of microbial biomass since the authors mention themselves that the cleaving of the polar head group is analogous to the cleaving of the polar phosphate group in PLFAs to NLFAs.
- How exactly are GDGTs superior to PLFAs (or NLFAs, see above)? It is mentioned in two different sections of the paper that GDGTS offer an improved time resolution of microbial biomass measurements to commonly used fatty acid biomarkers. At least to this reader the argumentation is not easily understood.
- The reliability of using brGDGTs as a biomarker for acidobacteria that prefer labile carbon is a bit obscure and could benefit from a more in-depth explanation. Is there conclusive evidence that bacteria producing brGDGTs are more likely to decompose labile carbon substrates?
- Archaea are mentioned to be of great importance in biogeochemical cycling in soils (the authors mention their importance in the buildup of necromass). Many studies report a drastically lower abundance of archaea in soils compared to bacteria and fungi. It would be good to add at least a brief explanation why the authors emphasize the role of archaea in soil organic matter buildup.
The aim of the study is stated to be investigating changes in microbial community structure by using a multi-proxy approach (i.e. PLFAs and GDGTs) to infer effects on decomposition and soil organic matter stability. While the microbial community drives microbial decomposition and affects soil organic matter stability, the study is not designed to assess changes in decomposition rates nor soil organic matter stability. The aim should be rephrased to focus on microbial community changes regarding afforestation. Possible implication of the alteration of soil microbial communities can be put into the discussion. Additionally, the aims of the study could include depth since the study in its current form uses subsoils in the title.
Material and Methods
Please explain the reason for the uneven sampling design (5 replicates for pastures and 3 for forest stands).
The replication for PLFAs is very small (2 replicates) and non-existent for GDGTs. This makes most of the discussion highly speculative and/or random since no reliable conclusions can be drawn from one data point.
A possible solution could be to widen the intervals of the sampling (0-10 cm, 20-30 cm etc.) which would result in 4 replicates for PLFAs and 2 for GDGTs.
Some of the parameters measured seem to be missing (e.g. fine root biomass). Please include how this data was obtained.
A brief explanation for the logic behind the nomenclature of the GDGTs is needed (e.g. roman numbers, letters and accents)Results
The results section would benefit of a clearer structure. Maybe an adaption could be to start with briefly describing the soil characteristics (e.g. soil C/N, pH etc.) of each vegetation type before diving deeper into PLFAs.
Interactive effects of depth and vegetation are often mentioned in the same sentence (e.g. line 185), which can become difficult to report and subsequently for the reader to understand. Depth has a well-studied correlation on soil microbial biomass and root mass, soil carbon and nitrogen concentrations and the effect of depth could therefore be reported separately (e.g. if there is a general decrease of all soil microorganisms in all vegetation types, this can be summed up, so the reader knows what to expect). Then a focus could be put on data that defers from this pattern (if there is any) or if vegetation types differed in the slope of the decrease or altered the depth distribution (e.g. C concentration more evenly distributed in one vegetation type than in the other vegetation types).
The results section is elongated a lot by reporting differences among the abundance of GDGT-subgroups between vegetation types. While in the material and methods section the usage of indices and their reasoning is stated, they are not used to full effect in the results. This could simplify reporting relative abundances of GDGTs subgroups (e.g. IIa and IIa’), as one could simply reference the indices themselves (given they are well explained in the materials and methods section).Discussion
The discussion could benefit from a restructuring. Currently, the discussion starts with describing the pasture in length and then discussing the forest stands separately. Since the aim of the study focuses more on the microbial communities in response to afforestation, it would be advisable to start discussing differences (or the absence of such) in PLFAs between pastures and forest stands right away. Depth needs to be discussed more (particularly if it is mentioned in the title) by highlighting differences among pastures and forest stands or the absence of such with depth. If differences occur only in subsoils, then this might be even discussed in a subsection or highlighted in the conclusion.
GDGTs (only worth including in this study if replication can be increased) could be discussed separately in a subsection but the point remains how they can be used to estimate microbial biomass since the core molecule seems to translate to microbial necromass rather than living biomass.
The general applicability of GDGTs in this study needs to be reevaluated. Particularly, the usage of brGDGT subgroups and the subsequently calculated indices are mentioned but add little information to the conclusion. For example, the lines 397-403 “The significant lower CBT5Me ratio in the old forest stand ages (55-year-old and 130-year-old) compared to the pasture and the 40-year-old forest reveals a different bacterial community towards bacteria who preferentially synthesize brGDGT with more cyclopentane moieties. Additionally, the IR6ME ratio was significantly higher in the pasture and in the 40-year-old forest compared to the older forest stand ages (Fig. 05b) indicating a higher relative abundance of 6-methyl over 5-methyl brGDGTs (De Jonge et al., 2024).” more or less reiterate the way these indices are calculated, however in what way these variations add information to the overall conclusion is not clear.
Additionally, there are many explanations for the variation in microbial communities with depth or among vegetation types that are vague and do not necessarily reflect current knowledge, (e.g. line 266 “particularly in bacterial biomarkers with increasing soil depth”, line 286 ”This might suggest a possible competition between AMF and saprotrophic fungi or Gram- bacteria”, see technical comments for explanation to why this seems counterintuitive).
There is a strong need to strengthen the discussion in general and revising some of the argumentations for variations in microbial communities (see technical comments for more detailed information).Conclusion
The conclusion focuses on differences in litter quality as the driving force of microbial community composition (PLFAs and GDGTs). Litter quality is not mentioned in the material and methods of this study but was assessed by the authors in another study in 2023. If this in fact is the main driving force of variation in microbial community composition, then the data must be included in the results and the methods.
Technical comments
26-29 please specify what kind of increase; with age? general? Only in subsoil?
41-44 it is difficult to follow the argumentation here, please explain how organic matter decomposition in deeper soil layers is enhanced by lower inputs of carbon
45-50 please give some more detail how litter quality shapes microbial communities
63-64 unknown or Acidobacteria? Please rephrase for clarification if this is a yet unknown species belonging to the phylum acidobacteria or only some of them are Acidobacteria but others are unknown etc.
64-67 “possibly feeding on root carbon sources” is probably meant to describe the organisms producing brGDGTs. Please rephrase for clarification, also mentioned the same way in 347
68 in a similar vein to in a similar way to
71-73 not sure if the turnover time refers to the total GDGT molecule (polar head and apolar core) or just the core. Likely for the core in which case this can’t be used as a biomarker for living biomass; needs clarification that this is a (archaeal necromass biomarker only) ; it is unclear how this is improves the time-integrated signal of soil microbial abundance compared to PLFAs
86 fungi are part of the soil microbiome
94-95 pastures mentioned here to contain less easily decomposable organic matter, but this is countering the overall argumentation
95-97 overall GDGTs or only branched ones? There is no argumentation found above for a preference of archaea for labile carbon sources
146-148 actinobacteria are also gram+ bacteria, labelling of gram+ bacteria must be changed to address this (e.g. rename gram+ to firmicutes, consult literature), interpretations in the discussion and report in the result section need to be addressed accordingly
150-151 One replicate per stand age can’t be used to interpret differences among forest stand ages and pastures, two replicates is also highly questionable
165-168 the F:B ratio is calculated by fungal PLFAs divided by bacterial PLFAs
177 would help understanding (and referencing later one) if the abbreviation IR6Me is mentioned in full length above.
185-187 pasture has a higher mean value than the 55-year-old forests for the 0-5 cm
210-213 “which was not observed in the pasture, the 40-year-old or 130-year-old forest” maybe this additional information is not needed since it is mentioned already that this is specific to 55-year-old forest
213-215 “common to all areas” but then mentioning 40-year-old forest specifically (in regard to what?) please rephrase, it would probably also be worth to mention the overall effect on fungi since relative effects of pH on bacteria and fungi are predicted to differ
217 Unfortunately I must strongly advise against using this data since one data point can’t be statistically evaluated; section was still reviewed for the sake of completeness
221-222 this is only true for the 130-year old forests which needs to be mentioned in this sentence to avoid confusion
224 it should say IIa instead of IIb
227-229 mentioned are only IIb’ and IIIb’ but not IIa’ and IIIa’, the concentrations only spike in 35-40 cm but besides that the major groups seem to follow the same trajectory then all other compounds (decreasing with depth)
264-266 fungi are often described to be decreasing stronger with depth since they are more associated with roots, the citations also don’t match the described observations (one of them focuses on microarthropods and neither focus on depth)
please add citations describing depth related distribution patterns of fungi and bacteria278 if still comparing to Francisco et al. (2016) then both investigate grass vegetations with grass species. Difficult to understand the point here
280-284 not clear to understand, root exudates are present in all soils only relative amounts vary, r2 instead of r
299-300 however you found an overall effect irrespective of the cyclisation ratio
308 the definition of substrate quality is questionable, soil pH does not describe substrate quality and vegetation cover may explain the amount of substrate available (although this has to be confirmed experimentally) but does not reflect on litter quality, carbon concentration of substrate is always organic and quality is therefore described through the C:N ratio already
314-315 the C:N ratio is known, right? Could be explored in the scope of this study
316-319 does this only apply to bacteria though? Citations seem again out of place (no bacteria studied in the first mentioned citation)
330 what do you mean by increased decomposition of old organic matter? Where is this reported
333-336 AFM to AMF; organic matter decomposition is seldomly seen in AMF, the cited paper reports much higher AMF values in pastures
346 the organisms producing brGDGTs not the molecule
384-397 highly speculative, there is little explanation why this should apply to the 40-year-old and 55-year old forests as well since temperature differences are only reported for pastures, if this can’t be backed up by further data it is advisable to drop this explanation
408-410 isoGDGTs are the only type of GDGT that is elevated in pastures, so archaea (additionally this means only an increase in archaeal necromass) is increased but they are not described here to be specifically associated to roots or labile carbon in comparison to other microbial groups, brGDGTs show not really a difference between pastures and 40 year and 55 year old forests according to the data presented
Figures
Information in the subtext should describe the unit, the meaning of the data points (e.g. mean) and the replication number
Supplementary
Table S1.
pH value and variation are exactly the same for 55-year-old forest and 130-year-old forest
Table S3.
NA value in 40-year-old forest in the wrong cell (35-40 missing AMF)
Citation: https://doi.org/10.5194/egusphere-2024-870-RC3
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