the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 02 Apr 2026
Testing the diffusion limitation hypothesis for declining methane uptake in forest soils
Abstract. Upland forest soils oxidize 22–38 Tg CH₄ yr⁻¹, roughly 5 % of the total atmospheric methane sink. A recent study documented a 53–89 % reduction at two long-term ecological research networks in the northeastern United States and attributed it to increased precipitation via diffusion limitation. We tested five predictions of that hypothesis against 27 years of chamber flux data from the Baltimore Ecosystem Study (BES, 1998–2025; n = 9,359) and 14 years from the Hubbard Brook Experimental Forest (HBR, 2002–2015).
Four predictions were not supported. At the individual-measurement scale, neither monthly precipitation nor direct soil moisture explained more than 1 % of CH₄ flux variance (R² = 0.0008 and 0.0055). While precipitation emerged as a significant interannual predictor when data were aggregated to annual-site means (β = 0.249, p = 0.002), it did not eliminate the residual multi-decadal decline (βyear = 0.211, p = 0.007). No seasonal moisture–flux structure matched diffusion predictions. Urban and rural BES forests diverged despite sharing a regional precipitation regime (Year×LandUse interaction, p = 0.007), and a residual temporal trend persisted after controlling for moisture, temperature, and spatial pseudoreplication (p = 0.002). A structural breakpoint at 2002 (BES) and a putative shift at 2011 (HBR) aligned with atmospheric deposition trends rather than precipitation. A fifth test, the Hubbard Brook calcium amendment, yielded a null result that does not discriminate between mechanisms but constrains methanotrophic recovery potential.
These results suggest that precipitation-driven diffusion limitation does not adequately account for the multi-decadal loss of CH₄ uptake at these sites and point toward chronic biological degradation, potentially through nitrogen-mediated inhibition of high-affinity methanotrophy compounded by structural changes from invasive earthworm activity.
Status: final response (author comments only)
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RC1: 'Comment on egusphere-2026-1723', Jiaxu Han, 03 May 2026
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AC1: 'Reply on RC1', Victor Edmonds, 05 May 2026
We agree with all seven helpful and constructive points and will incorporate them in the revised manuscript. The comments are well-targeted: several flag tonal adjustments that improve scientific rigor, two surface claims that were under-emphasized in the current draft and warrant clearer treatment, and the remainder address terminology and figure clarity.
A brief response to each follows (full text changes will appear in the revised version).
- Agreed. The abstract and introduction will explicitly distinguish the precipitation-driven (climatic) diffusion limitation hypothesis under test from the structural diffusion mechanism (earthworm/soil compaction) discussed later. The two mechanisms operate on different timescales and through different physical pathways.
- Agreed. The abstract will note that the in-situ VWC record (2011–2020) postdates the 2002 BES structural breakpoint and therefore characterizes post-decline rather than pre-decline soil moisture conditions.
- Agreed. The same caveat will be added at the first introduction of the VWC dataset in the Methods section to establish appropriate context for the mechanistic test.
- Agreed. Without direct microbial abundance data (e.g., pmoA gene surveys), the inference from the WS1 calcium amendment null result to biological control is indirect. The phrasing will be softened to "a highly plausible hypothesis consistent with existing biochemical pathways," preserving the biochemical logic while also acknowledging the limitation.
- Agreed. Given the small post-break sample (n = 4, or n = 2 if truncated), "putative shift" is the appropriate phrasing. We will propagate this language consistently through the abstract and body wherever the 2011 HBR breakpoint is referenced.
- Agreed. The current figure (and caption) could greatly benefit from this visual representation and breakout. Vertical dashed lines marking the 2002 (BES) and 2011 (HBR) breakpoints will be added to both panels of Figure 5 to allow direct visual alignment with the atmospheric wet deposition trends.
- Agreed, and we appreciate the recognition/highlight of this point. The return-to-baseline framing will be added as a paragraph in the Conclusions (Section 5), since it offers an alternative interpretation of the long-term trend that warrants more direct treatment rather than being confined to the Discussion.
We will submit the revised manuscript with these changes incorporated.
Citation: https://doi.org/10.5194/egusphere-2026-1723-AC1
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AC1: 'Reply on RC1', Victor Edmonds, 05 May 2026
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RC2: 'Comment on egusphere-2026-1723', Anonymous Referee #2, 04 Jun 2026
This manuscript tackles an important and timely question: whether the long-observed decline in forest soil methane uptake at the Baltimore Ecosystem Study (BES) and Hubbard Brook Experimental Forest (HBR) can be explained by precipitation-driven diffusion limitation. The author challenges a prominent framework, the precipitation-driven diffusion limitation hypothesis proposed by Ni and Groffman (2018b), by analyzing an impressive, high-density long-term dataset spanning 27 years at the Baltimore Ecosystem Study (BES) and 14 years at the Hubbard Brook Experimental Forest (HBR). Also attempts multiple independent tests of the diffusion hypothesis. By demonstrating that neither monthly precipitation nor direct volumetric water content (VWC) accounts for more than 1% of instantaneous flux variance, the manuscript effectively demonstrates that climatic diffusion limitation is insufficient to explain the secular decline.
The manuscript raises an important and timely question regarding the mechanisms underlying the long-term decline in forest soil methane uptake. However, I am not fully convinced that the analyses presented here adequately test the diffusion limitation hypothesis itself. The study demonstrates that monthly precipitation explains very little variation in methane flux, but precipitation is only an indirect proxy for diffusion processes. Diffusion limitation is fundamentally governed by air-filled pore space and soil gas diffusivity, whereas direct soil moisture measurements are available only for 2011–2020, after the inferred BES breakpoint. Therefore, the results provide stronger evidence against a simple precipitation-based explanation than against diffusion limitation as a mechanistic control. I recommend that the authors moderate the title and conclusions accordingly and more clearly distinguish between rejecting precipitation as a predictor and rejecting diffusion limitation as a process. As currently written, some conclusions appear stronger than the data support.
Some of my concerns are listed below:
1. The manuscript provides convincing evidence that precipitation alone explains little of the observed variation in CH₄ uptake. However, I am not fully convinced that this necessarily constitutes a rejection of the diffusion limitation hypothesis. Because diffusion is controlled by air-filled porosity and gas diffusivity rather than precipitation per se, and because direct soil moisture observations are only available for a limited period, the conclusions should be framed more cautiously. The evidence appears stronger for rejecting a simple precipitation-based explanation than for rejecting diffusion limitation as a mechanistic driver.
2. The discussion increasingly advances specific alternative explanations for the observed decline in CH₄ uptake, including nitrogen saturation, methanotroph collapse, irreversible biological degradation, and earthworm-mediated destruction of methanotrophic habitat. While these mechanisms are plausible and worthy of consideration, the current manuscript does not provide direct evidence to support them. No measurements of methanotroph abundance, USCα abundance, pmoA gene abundance, microbial community composition, earthworm density, or methane oxidation potential are presented. As a result, the evidence remains largely circumstantial, and several interpretations extend beyond what can be directly inferred from the data. In several places, speculative mechanisms are presented in language that implies causal inference rather than hypothesis generation. For example, the statement that “urban sites have stabilized at a biological floor” is an interesting interpretation, but no direct evidence is provided demonstrating the existence of such a threshold or floor. Similar concerns apply to discussions of microbial community collapse and irreversible degradation. I recommend reframing these sections as hypotheses that are consistent with the observed patterns rather than conclusions supported by direct evidence. Throughout the Discussion, more cautious language such as “may be consistent with,” “could reflect,” or “is compatible with” would be more appropriate than stronger terms such as “indicates,” “demonstrates,” or “supports.”
3. The manuscript acknowledges that the 2002 breakpoint was first identified using the PELT changepoint algorithm and then subsequently used to divide the dataset into pre- and post-breakpoint periods. This same partition is later used to demonstrate a stronger moisture–flux relationship before the breakpoint. Such an approach introduces a risk of post-hoc inference, because the structure identified from the data is subsequently used to generate additional evidence from the same dataset. The manuscript appropriately notes this limitation, but the interpretation remains stronger than the statistical support appears to justify. In particular, the reported permutation test (p = 0.057) suggests that the evidence for a meaningful difference in moisture–flux coupling before and after the breakpoint is suggestive rather than conclusive. Given this uncertainty, I recommend presenting these analyses more cautiously and avoiding strong mechanistic interpretations based on the breakpoint partition. Alternatively, the pre/post-breakpoint moisture analysis could be moved to the Supplementary Material, where it would still provide useful context without carrying disproportionate weight in the overall argument.
4. The changepoint analysis represents a central component of the manuscript's argument, yet the robustness of the inferred breakpoints is not fully characterized. Although the manuscript reports sensitivity analyses across a range of penalty values, a single breakpoint estimate is ultimately emphasized, and uncertainty surrounding breakpoint timing is not quantified. Confidence intervals or other measures of breakpoint uncertainty are not provided. In addition, the inferred breakpoint at Hubbard Brook is based on a very limited post-breakpoint record, with only four years of observations available after 2011. This substantially limits confidence in the existence and timing of a distinct post-break regime.
Because the Discussion repeatedly uses the identified breakpoints as evidence supporting biological interpretations, a more rigorous evaluation of breakpoint uncertainty is needed. I encourage the authors to provide confidence intervals for breakpoint estimates where possible, compare results across alternative changepoint detection methods, expand the sensitivity analyses, and more explicitly discuss the limited statistical power associated with the short post-breakpoint period at Hubbard Brook. These additions would substantially strengthen confidence in the conclusions drawn from the changepoint analyses.
5. The manuscript repeatedly interprets the low explanatory power of precipitation and soil moisture as evidence against diffusion limitation. However, chamber-based methane flux measurements are inherently noisy and influenced by multiple interacting controls operating at different temporal and spatial scales. Consequently, very low R² values may not necessarily indicate that moisture is unimportant. The authors should discuss whether low explanatory power is expected in observational chamber datasets and provide additional context from previous studies reporting moisture–flux relationships in upland forest soils.
My specific comments are as below:
1. Line 184 vs. Line 715 (Data Consistency): In Section 3.1, the paired VWC-flux regression lists n = 2,415. However, in Appendix A3 (Line 714), the text mentions "For direct VWC measurements n = 301". Please verify if the n=301 in the appendix refers to a specific subset or aggregated scale, and explicitly clarify this discrepancy so reviewers do not flag it as an inconsistency.
2. Line 201 (The 2002 Pre-Breakpoint Split): The author notes that the pre-2002 precipitation-flux relationship was 7x stronger than the full record, but the permutation test yielded p = 0.057. Adhering to the philosophy of Gelman and Stern (2006) cited elsewhere in the text, a p = 0.057 should be treated with strict caution.
3. Figure 5 Improvements: Figure 5 overlays deposition chemistry with CH4 trends. To maximize its visual impact, add vertical dashed lines corresponding to the PELT-detected structural breaks (2002 for BES, 2011 for HBR). This will allow the reader to visually evaluate the multi-year lag between peak deposition loading and sink collapse.
4. Section 4.12 (Testable Predictions): The inclusion of specific, molecular eco-meteorological blueprints (pmoA qPCR, transcriptomics, active vs. relic DNA) is a good way to end a purely observational/modeling paper. Consider adding a brief call-to-action inviting the broader LTER network communities to open their soil archives to validate these predictions.
Citation: https://doi.org/10.5194/egusphere-2026-1723-RC2 -
AC2: 'Reply on RC2', Victor Edmonds, 07 Jun 2026
We thank Referee #2 for a rigorous and constructive review.
On the overarching point (that the analyses more strongly reject a precipitation-based explanation than diffusion limitation as a process), we agree, and we will scope the claim accordingly.
The manuscript does not argue against diffusion as the proximate control on CH₄ uptake; gas transport through air-filled porosity is the rate-limiting mechanism in both the hypothesis under test and the alternatives we raise. What the manuscript tests, and does not support at these sites, is the specific attribution of the secular decline to precipitation as the driver of reduced diffusivity.
The distinction is between a reversible, climatically driven reduction in diffusivity (which should track soil moisture) and an irreversible, one-directional reduction (which would not). The observed decoupling of flux from moisture is consistent with the latter.
We will update the title, abstract, and conclusions (and other applicable areas of the manuscript) so that the claim under test (precipitation as driver) is clearly separated from diffusion as a mechanism, which we do not reject.
Major comments
- The precipitation-driven (climatic) hypothesis under test will be distinguished throughout from diffusion as a general transport mechanism, and from structurally mediated reductions in diffusivity. We will also note that the direct VWC record (2011–2020) postdates the 2002 BES breakpoint and therefore characterizes post-decline conditions, which limits its reach as a test of pre-decline diffusion control.
- The alternative mechanisms in the Discussion will be reframed as hypotheses consistent with the observed patterns, not as conclusions, given that no microbial, molecular, or earthworm-density measurements are presented. We will replace causal language (“indicates,” “demonstrates,” “supports”) with “may be consistent with,” “could reflect,” or “is compatible with,” and will remove “biological floor” as an asserted finding. We will also clarify that these candidates span two distinct mechanistic regimes that the present data cannot separate: a structurally driven reduction in diffusivity, which would preserve the transport-limited (diffusion) regime, and a reduction in oxidation capacity (e.g., methanotroph community change, nitrogen saturation), which would shift the system out of the diffusion-limited regime entirely. The manuscript will present these as open questions rather than adjudicating between them.
- We will temper the language around the pre/post-2002 moisture–flux comparison and frame it explicitly as suggestive and subject to post-hoc inference, consistent with our reporting of p = 0.057 rather than treating it as significant. We propose to retain the analysis in the main text, since whether moisture coupling weakened across the decline bears directly on the paper’s argument, but to present it with reduced interpretive weight and an explicit statement of the circularity limitation. (We also note for the referee that an interaction model fit on the full record without subsetting — Precipitation × Post-2002 — returns a non-significant interaction, p = 0.24; this is consistent with the permutation result and is reported in the Supplement as an independent check that does not rely on the post-hoc split.)
- The revision will add (i) bootstrap confidence intervals on breakpoint timing, (ii) a comparison across alternative changepoint detection methods, (iii) expanded penalty sensitivity analyses, and (iv) explicit discussion of the limited statistical power at Hubbard Brook given the short post-2011 record.
These analyses have been carried out. The BES breakpoint timing has a 95% bootstrap interval of [2000, 2006] and the HBR breakpoint [2011, 2012]; the intervals do not overlap, so the asynchrony between the two sites is preserved. The BES break at 2002 is recovered by four of five detection algorithms (PELT, binary segmentation, bottom-up, and dynamic programming; the window-based method places it at 1999) and the 2002 break is present across penalty values from 0.01 to 2.0 (wider than the range currently reported), with secondary BES breakpoints (2007, 2017) appearing only at lower penalties. The HBR break is recovered by all five algorithms and is present across penalties from 0.05 to 1.5. We will report the bootstrap intervals in place of bare point estimates. On the Hubbard Brook power analysis: the observed post-2011 shift is statistically clear (pre-break n = 10, post-break n = 4; Cohen’s d = 3.35; two-sample p = 0.0001), so the limitation is not that the break may be a low-power artifact. Rather, a four-point post-break regime (two if the final years are truncated) cannot have its level or stability characterized, and only large shifts (minimum detectable d ≈ 1.8) would be detectable at all. This is why we describe the 2011 break as a putative shift requiring confirmation through extension of the record. We have also harmonized the supplementary changepoint sensitivity analysis with the main analysis so that both use the same annual series and breakpoint-labeling convention. - Agreed, with one clarification. We will add discussion of the inherent noise in chamber-based CH₄ flux measurements and the expectation of low instantaneous R² in observational datasets, with context from prior upland forest studies. The argument rests on the secular decline failing to track moisture, which constrains the driver of the decline to be something other than the reversible hydrological control. We will make this distinction between instantaneous variance and the multi-decadal trend clear.
Specific comments
- On verification: re-running the analysis confirmed that the Appendix S3 figure of n = 301 was a code issue rather than a distinct subset. The site-name mapping was omitted from the supplemental script, which retained only one (ORUR) of the five VWC sites. Corrected on the full paired dataset (n = 2,415), the quadratic VWC term remains non-significant (p = 0.72; quadratic R² = 0.56% vs. linear 0.55%), so the robustness check returns the same conclusion (a quadratic form does not rescue the diffusion explanation), now on the complete We have updated the supplemental script so the code reproduces the corrected value, and will correct the Appendix S3 figure and the Methods description of the VWC–flux match (which is performed at monthly resolution: mean VWC per site-month matched to chamber measurements) in the revision.
- Addressed under major comment 3. The p = 0.057 result will be treated with caution and not interpreted as significant.
- Vertical dashed lines marking the breakpoints (2002 for BES, 2011 for HBR) have been added to both panels of Figure 5, allowing visual evaluation of the lag between peak deposition loading and sink decline.
- Agreed, and we appreciate the suggestion. We will add a brief call in Section 4.12 inviting the broader LTER network to make soil archives available for validating the molecular predictions.
These changes will be incorporated in the revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-1723-AC2
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AC2: 'Reply on RC2', Victor Edmonds, 07 Jun 2026
Data sets
Analysis code for "Evidence for Biological Control of the Declining Forest Methane Sink" Victor Edmonds https://doi.org/10.5281/zenodo.18944403
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The manuscript provides a highly rigorous and analytically sound evaluation of the diffusion limitation hypothesis using long-term data from the BES and HBR networks. The statistical methodologies are robust, and the paper is logically structured. However, a few terminological clarifications, tonal adjustments regarding inferred biological mechanisms, and graphical enhancements would further elevate the manuscript. More importantly, two overarching issues should be addressed to strengthen the scientific rigor of the study. First, the conceptual framing of the “diffusion limitation hypothesis” requires clearer specification, particularly in distinguishing precipitation-driven (climatic) diffusion from structurally mediated diffusion processes discussed later in the manuscript. Second, several key interpretations—especially those related to biological mechanisms and long-term drivers—are based on indirect inference from observational data and would benefit from more cautious wording and clearer acknowledgment of their limitations.
Here are my specific comments:
1. In the abstract and introduction, make sure it is clearly stated that the manuscript is testing the "precipitation-driven (climatic) diffusion limitation hypothesis." Because they also discusses "structural diffusion limitation" caused by invasive earthworms, so two mechanisms should be clearly distinguished to avoid confusion.
2. The study's in-situ volumetric water content (VWC) data from 2011-2020 spans after the 2002 structural breakpoint at BES. This should be mentioned in the abstract to avoid over-interpretation of the VWC results in the context of pre-decline conditions.
3. Line73: When first introducing the VWC dataset (2011-2020) in the Methods section, it would be helpful to explicitly mention upfront that this timeframe occurs after the established 2002 BES breakpoint, setting the appropriate context for the mechanistic test presented later in the paper.
4. Line246 Regarding the WS1 calcium amendment, stating that the null result is "positive evidence for biological control" is too strong. While the biochemical logic (liming increases pH/nitrification, thus inhibiting acidophilic methanotrophs) is sound, without direct microbial abundance data (e.g., pomA gene surveys), this remains speculative. Please soften the phrasing to "a highly plausible hypothesis consistent with existing biochemical pathways."
5. Line314 The author rightly and transparently acknowledges that the 2011 HBR breakpoint leaves only 4 data points in the post-break regime (and only 2 if truncated). Please ensure that this is consistently referred to as a "putative shift" throughout the entire manuscript—including adjusting the wording in the abstract (around Line 13)—to maintain a rigorous statistical tone.
6. Fig.5: To help readers visually align the atmospheric wet deposition trends with the sink collapses, please add vertical dashed lines to both panels in Figure 5 indicating the respective structural breakpoints (2002 for BES; 2011 for HBR).
7. Line445 The "return-to-baseline" hypothesis—suggesting that late-20th-century acid deposition artificially stimulated methane uptake, and the current decline is actually a normalization—is a brilliant, paradigm-shifting insight. Because it fundamentally reframes the ecological narrative, consider briefly mentioning this alternative hypothesis in the Conclusions (Section 5).