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).

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.