the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 12 Jun 2026
Old organic matter in temperate forest soils is very nitrogen-rich
Abstract. Soil organic matter (SOM) is important for Earth’s climate regulation and primary production. Here we tested the hypothesis that old SOM fractions are rich in organic nitrogen given the high affinity of organic nitrogen compounds to interact with mineral surfaces. For this purpose, we studied temperate broadleaf and coniferous forest soils located in Sweden. We used ramped thermal fractionation to obtain persistent SOM fractions, and we evaluated the persistence using 14C. The results show that old SOM fractions in the temperate forest soils are very nitrogen-rich, indicating that organic nitrogen compounds persist for a long time in soil. A larger proportion of the total organic nitrogen than of the total organic carbon was found in the old SOM fractions, suggesting that organic nitrogen compounds decompose on average more slowly than nitrogen-free organic compounds. The size of the old SOM fractions was correlated with the soil clay content but did not differ significantly between broadleaf and coniferous forests, suggesting that association with minerals rather than forest type or organic matter quality affect the persistence of SOM. This study has important implications for element cycling as it demonstrates that nitrogen in temperate forests persists for a long period in SOM.
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Status: final response (author comments only)
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RC1: 'Comment on egusphere-2026-3238', Anonymous Referee #1, 23 Jun 2026
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AC1: 'Reply on RC1', Marie Spohn, 25 Jun 2026
Please find our replies in the attached document.
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RC3: 'Reply on AC1', Anonymous Referee #1, 10 Jul 2026
The authors defended their thermal approach with the fact, that only organic nitrogen is involved in the Maillard reaction and it is not converted into inorganic nitrogen. At the same time they mentioned, that the highest reaction rates are already at 140-160°C. Figure 2 clearly shows, that very little organic N is lost after ramped heating. My point is, that the lower heating transformed (condensated) the organic N into more thermo-stable forms (exactly as reported in the mentioned paper), which then survived the higher temperatures, while C did not. I therefore still have a fundamental doubt, that the approach can be used to test the interesting hypothesis of the authors. I recommend to test it with an alternative approach to exclude a potential artefact.Â
Citation: https://doi.org/10.5194/egusphere-2026-3238-RC3 - AC3: 'Reply on RC3', Marie Spohn, 12 Jul 2026
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RC3: 'Reply on AC1', Anonymous Referee #1, 10 Jul 2026
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AC1: 'Reply on RC1', Marie Spohn, 25 Jun 2026
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RC2: 'Comment on egusphere-2026-3238', Anonymous Referee #2, 09 Jul 2026
I greatly enjoyed reading this manuscript. The authors use thermal ramping to separate different stability fractions of SOM and the analyse them for carbon isotopy, C and N to investigate the relationship between SOM stability, C age and N content. They show that thermal ramping is a useful method for separating SOM pools. They find that more stable and older SOM is N-rich and discuss the mechanisms well. The manuscript is interesting and the approach seems to be useful, and refreshing, because density fractionation has become almost set in stone for separating SOM stability fractions. The findings about ON-richer stable SOM are scientifically interesting, the proof is novel and relevant for many disciplines across ecology. The finding that SOM age is related largely to clay content might not be most surprising, but is demonstrated clearly; a valuable finding. The finding that forest type does not affect SOM sequestration and its ON is novel and needs more discussion. The assumptions and interpretations are valid, methods and statistics are robust. The manuscript is written clearly and confidently, resulting in good style. There are not many references and they are repeated (expect in the part about ON biogeochemistry which is fine), however this might be acceptable because the study is specific.
Even though this is a short format and not an applied study, I would have wished to read about how come it is so well established that broadleaf versus forests have different SOM quality, while the authors show SOM sequestration and ON is not controlled by forest type. It is, after all, in the first hypothesis. I leave it to the authors to figure out how to reduce this complicated topic and maintain the manuscript concise.
Structure comment: The introduction says that coniferous and broadleaved forests have different SOM quality. To the reader this implies that ON, too, will be different. Then, your alternative hypothesis is that the ON in old SOM will be same in coniferous and broadleaved forests.
20/25: Remove Hence.
170: Missing dot.185: … SOM that differs […] from other SOM pools. Suggest adding why this is practical and biogeochemical significance of the different SOM pool.
Citation: https://doi.org/10.5194/egusphere-2026-3238-RC2 - AC2: 'Reply on RC2', Marie Spohn, 12 Jul 2026
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RC4: 'Comment on egusphere-2026-3238', Anonymous Referee #3, 15 Jul 2026
While the concept presented in this manuscript is highly compelling and represents a potentially novel insight when viewed in broad strokes, there are several shortcomings to both the experimental approach and its interpretations as well as to the manuscript itself.
The manuscript:
- The word "very" in the title should be omitted. Adverbs are challenging in a quantitative domain. that is, what does "very" mean in terms of N concentration? The word is ambiguous and doesn't provide additional information.
- This is a short communication, that is actually shorter than it appears because a great deal of its content is repeated several times. When the repetition is removed, there is not much left. This is unfortunate because there are many angles that need to be unpacked and elaborated in the interpretation of the results before the reader might have much confidence in the conclusions.
- While the manuscript is readable, it could use some fine-tuning to make the English more natural and fluid.
- No paragraph should be a single sentence. Too many sections are broken up into unnecessarily into multiple too-short paragraphs.
- The authors frequently use a sentence structure that requires the use of "respectively" throughout the manuscript. The structure "A, B, C are related to X,Y,Z, respectively" requires the reader to perform mental matching and disrupts the fluidity of reading. Instead, the sentence could be structured as "A is related to X, B to Y, and C to Z." This improves the reading experience.
- The authors need to be careful about distinct diction for "fraction" and "pool". Generally, "pool" is used to refer to a non-tangible, non-measured, modeled collection, while "fraction" is a tangible"/"real", measured, physical entity.
- The methods section could be re-structured to distinguish between characterization and analysis. That is, measurements of total soil organic C and N and soil texture might come first in the order because hey are basic characterization measurements. These would then be followed the thermal fractionation procedure (perhaps as a separate subsection) and the isotopic analysis.
- The section on statistical analysis needs elaboration. What variables are being examined? Which are dependent and which are independent?
Conceptual/Scientific/Experimental:
- The authors cite Sanderman & Grandy (2020) and Stoner et al (2023) in the background on thermal analysis coupled with isotopic analysis, but while the method might be slightly different, these studies are pre-dated by those of Lopez-Capel et al. (2005, 2006) that coupled ramped combustion with 13C and Plante et al. (2013) that coupled ramped combustion to 14C.
- If I understand the approach correctly, samples are subjected to ramped combustion to a fixed temperature and the residue is used for subsequent analyses. But what happens to the samples once the threshold temperature is reached? Are they removed from the instrument immediately? Whta is the cooling rate? How long are they exposed to elevated temperatures?
- The authors seem to implicitly treat C and N are independent pools in some arguments, or implicitly link the behaviour of the two in other arguments. Which is it? That is, just because the C is old (indicated by 14C) what makes the N old (indicated by ?). Alternative, are compounds rich in N-containing known to be more thermostable? The interpretation as written seems to confound biochemical-thermal stability with mineral-association-stability, (both) in relation to thermal stability. There is a lot that needs to be unpacked here before there can be any confidence in the conclusions.
- I'm not sure there is sufficient understand of the behavior of N-containing compounds to assume that they oxidize at the same rate/temperature as non-N containing compounds. While this may be an underlying assumption or requirement, it is not adequately elaborated. There may be something to be learned from examining the pyrogenesis literature (e.g., Knicker (2010, Org Geochem); DeLaRose (2011, SBB).
- The discussion is centered on two rather strong assertions that are written in a highly speculative tone. How can these assertions be supported? Are they known to be true? Can they be tested? There is much elaboration needed here.
- I found the correlations with clay content compelling, but it was unclear why pH was included in the statistical models. pH as a control on microbial activity is a much different mechanisms that pH as a driver for mineral-association. There may be some confounding of cause and effect here.
- In terms of these statistical analysis, I believe the authors may be using "correlation" and "regression" - but should not. Theauthors should consult papers by Webster on the distinction (1997, EJSS and 1989, SUM). In addition, the improvement of model performance with the addition of pH to clay should be tested using model selection methods (e.g., AIC).
Overall, the outcomes of the study seem intuitive and compelling, but as the saying goes "the devil is in the details", and this manuscript lack a great deal of details that are needed for the reader to have sufficient confidence in the conclusions reached based on the collected evidence.
- AC4: 'Reply on RC4', Marie Spohn, 18 Jul 2026
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I reviewed this short, but very interesting manuscript by Spohn et al., who used thermal oxidation and radiocarbon dating to show that old organic matter in Swedish forest soils is strongly enriched in nitrogen. The approach taken is generally interesting, but the authors would need to proof, that the N-enrichment is not an artefact of the thermal oxidation. This is most likely very difficult. The so-called Maillard reaction, which is well known in the pyrogenic carbon community and also food chemistry, is the condensation of sugars with amino acids under high temperatures (see e.g.: Nitrogen Enrichment during Soil Organic Matter Burning and Molecular Evidence of Maillard Reactions | Environmental Science & Technology). Although thermal oxidation might be a way to isolate biogeochemically meaningful organic matter fractions, they do not remain unchanged. The KCL extraction done by the authors to quantify the amount of mineral nitrogen in the samples after thermal fractionation is not enough, because here its about the formation of aromatic nitrogen. Unfortunately, the methodological choice here is most likely not suitable to test the hypothesis of the authors. As a consequence, the manuscript needs to be rejected at that stage. Â A simple physical fractionation might have been the better choice to separate younger and older OM.
Apart from this fundamental comment, I’d like to mention that although short papers are nice to read, I found this one a bit too superficial in some parts. Surely, the authors mentioned a couple of times, that N-rich organic compounds might have a higher affinity to be sorped and stabilized, but readers would probably like to get some more background and deeper understanding on that. Also, the step of organic matter transformation (e.g. by microbes) is somewhat missing. We know that a substantial part of mineral associated OM consists of microbial necromass, which is per se quite enriched in N. Although the authors have no data on this, there could be more in-depth discussion on the different stabilization pathways. I also miss a bit of an implications section in the discussion (what does that mean for the ecosystem, for the different biogeochemical cycles, how far can you generalize these results, and who should care about them). Also, a proper conclusions section is missing.
Specific comments:
Line 12: It could also indicate, that organic matter becomes enriched in its transformation processes and that more processed organic matter persists longer.
Introduction: Maybe at least mention the ‘microbial carbon pump’ and how this relates to N
Line 53: Could you please elaborate a bit more on your exclusion criteria of Podzols? To avoid strong eluviation, you could have selected via OM content.
Line 58: Why larger than 55 years?
Line 74: Why so restricted to the 0-10 cm layer?
Line 75: So you took the soils from the archive? Could be mentioned.
Line 78: Why 35°C? This seems rather low.
Line 1745ff: This whole section seams to belong to the section above (on thermal fractionation). Maybe move upwards?
Figure 2: I don’t really like the x-axis names. Soil, 325°C, 400°C. Please consider changing.Â