the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 28 Jul 2026
Effects of enhanced rock weathering on soil gas fluxes across UK land uses
Abstract. Enhanced rock weathering (ERW) is a proposed carbon dioxide (CO2) removal strategy via the application of crushed silicate rocks to accelerate the natural breakdown of silicate minerals, permanently trapping atmospheric CO2. Application of rock dust may alter soil properties, such as pH, with potential consequences for soil trace gases fluxes relevant to climate forcing and air quality. However, previous ERW studies have focused mainly on the principal greenhouse gases, while broader trace gas responses remain poorly constrained. This laboratory study presents measurements of nitric oxide (NO), ammonia (NH3), carbon monoxide (CO), hydrogen (H2) and volatile organic compounds (VOCs), as well as CO2, methane (CH4) and nitrous oxide (N2O), from control and ERW-treated soils collected from arable, grassland and newly planted broadleaf and conifer forest field trials in the UK. Soils were sieved, repacked and rewetted for laboratory measurements. A dynamic air-flow-through chamber system, equipped with a high-resolution multi-gas analyser and a proton-transfer-reaction mass spectrometer, was used to measure N2O, NO, NH3, CO, and VOCs between 5 and 25 °C. CO2 and CH4 fluxes were measured online at 20 °C using a closed-loop chamber method, and H2 fluxes were measured by discrete sampling from static chamber headspace using gas chromatography. ERW-associated differences varied among gases and soils, with no consistent response across all incubated samples. The reported treatment differences included lower CO2 emissions in both forest soils, greater CH4 uptake in broadleaf forest soil, higher NO emissions in grassland soil, and changes in CO and hydrocarbon fluxes in forest soils. NH3 and H2 fluxes showed no statistically significant treatment responses, and no individual VOC remained significantly different after correction for multiple testing. Overall, rock dust application had limited and inconsistent impacts on trace gas fluxes across the soils examined in this snapshot study. Longer-term measurements at ERW field trials are needed to examine how these responses vary seasonally and evolve as the applied materials continued to weather. These measurements should be accompanied by in-depth soil characterisation and microbial analyses to elucidate the complex relationships between ERW treatment and trace gas fluxes. This evidence is needed to assess the full climate, air-quality and environmental implications of large-scale ERW deployment.
Competing interests: At least one of the (co-)authors is a member of the editorial board of Biogeosciences.
Publisher's note: Copernicus Publications remains neutral with regard to jurisdictional claims made in the text, published maps, institutional affiliations, or any other geographical representation in this paper. While Copernicus Publications makes every effort to include appropriate place names, the final responsibility lies with the authors. Views expressed in the text are those of the authors and do not necessarily reflect the views of the publisher.- Preprint
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Status: open (until 18 Sep 2026)
- RC1: 'Comment on egusphere-2026-4380', Anonymous Referee #1, 09 Sep 2026 reply
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RC2: 'Comment on egusphere-2026-4380', Anonymous Referee #2, 09 Sep 2026
reply
This laboratory study measured fluxes of the principal greenhouse gases (CO2, CH4 and N2O) together with a broader suite of trace gases (NO, NH3, CO, H2 and VOCs) from ERW-treated soils collected at three UK field trials spanning arable, grassland and newly planted broadleaf and conifer forest. The measurements show largely inconsistent ERW treatment responses across land uses. Extending the analysis beyond the principal greenhouse gases is novel and important, since it allows the implications of ERW to be assessed not only for climate forcing but also for air quality. The dataset is valuable and the manuscript is well organized and clearly written. I have the following comments and suggestions, which I hope will help the authors strengthen the manuscript further, and I believe it should be suitable for publication once these points are addressed.
Introduction:
L33–40: A brief statement on the current maturity of ERW as a CDR approach (e.g., still at the early field-trial stage, with monitoring, reporting and verification (MRV) under active development) would help position the study, since quantifying this wider set of gas fluxes is directly relevant to the MRV of such approaches. The recently released third edition of The State of Carbon Dioxide Removal (Edwards et al., 2026) would be a useful reference here, and Schiedung et al. (2026) review the uncertainties of ERW.
L37–38: The phrase "the resulting alkalinity of these basic cations" reads as chemically imprecise. Alkalinity is generated by proton consumption during mineral dissolution, with charge balance maintained by bicarbonate; cation release and alkalinity generation are therefore two descriptions of the same charge-balanced process, rather than a property of the cations that subsequently converts CO2. Please consider rephrasing this sentence.
L39: The statement that bicarbonate remains "in groundwater and oceans for upwards of 10,000 years", read together with "permanently trapping atmospheric CO2" (L12), may overstate the transfer efficiency of captured CO2 as the form of (bi)carbonate. Losses along the land–ocean continuum, including riverine CO2 evasion and secondary CaCO3 precipitation, reduce the fraction of soil-generated alkalinity that ultimately reaches long-term marine storage. A single caveat sentence would be sufficient to address this.
L83–85: The Introduction closes with an aim but no explicit hypotheses, although the Discussion is largely organized around pH-mediated mechanisms. Readers would benefit if the expected direction of response for each gas, or at least for the principal greenhouse gases, under increased soil pH were stated here. This would sharpen the design and make the later discussion even more meaningful, for example the interesting finding that NO responses contrast with model predictions (L466–467).
Methods:
General: Beyond the field pH shift, were any weathering-extent indicators measured for the incubated soils, such as the residual feedstock fraction or exchangeable Ca2+ and Mg2+? If so, it would be very helpful to report them; if not, please state this as a constraint on inferring the state of weathering from this experiment.
L115: The grassland soil was collected in December 2023 but measured in April 2025 (L133–136), roughly 16 months of storage compared with about two months for the other sites. How, and under what conditions, was this soil stored, and can its quality be assumed to have been maintained over such a long period? Reporting the storage duration and conditions for each site would also improve reproducibility.
L125: The metabasalt feedstock applied at the forest site contains 1–14 % calcite, which is not a negligible fraction at the upper end of that range. The forest-soil responses may therefore partly reflect a carbonate rather than silicate weathering. Please discuss whether the observations can be attributed to silicate ERW specifically, or whether they should be framed somewhat more cautiously as effects of rock powder application including its carbonate fraction.
L153–156: Could you briefly explain the choice of the 5–25 °C range, presumably to span typical UK topsoil temperatures, given the site mean annual temperatures of 9.2–11.4 °C in Table 1? A related point: temperature affects not only microbial rates but also abiotic processes, including mineral dissolution kinetics, CO2 solubility and carbonate equilibria, so the observed temperature responses conflate biotic and abiotic effects, particularly for the calcite-bearing forest feedstock. If no further data are available to separate these contributions, it would be good to acknowledge this in the Discussion.
L163: The flow rate of "~4 m3 s-1" appears too high for such experimental setups, corresponding to 4,000 liter per second. Please confirm the value and units actually used in Equation 1, since the calculated flux magnitudes scale linearly with Q. The same value is quoted again at L400 in the discussion of NH3 adsorption, so both of these numbers may need to be updated.
Results:
L227–229 (Figure 1; Table 2): The grassland fluxes are markedly more variable than those of the other sites, and for CH4 and N2O the control samples are notably more variable than the ERW samples (e.g. CH4: 442 ± 159 vs. 46 ± 11 pg g-1 h-1). Could this be related to the comparatively long storage of the grassland soil and to the rewetting procedure? A brief comment in the text would be helpful.
Discussion:
L355–357: Because the soils were air-dried rather than oven-dried (drying at 105 °C was applied only to sub-samples for gravimetric water content, L132–133), the incubated soils remained biologically active. Air-drying induces dormancy and kills part of the microbial biomass, and rewetting reactivates the surviving community, typically producing a mineralization pulse. The manuscript invokes such a rewetting pulse to explain the grassland N2O variability, but drying–rewetting artefacts are not considered for the other gases, nor is the possibility that control and ERW communities respond differently to this disturbance. I would suggest discussing drying–rewetting effects as a general limitation applying to all measured gases. In addition, sieving to 2 mm (L132) will have removed part of the feedstock applied at particle sizes of up to 4 mm in the 2020 forest application (L127), altering the effective dose in the incubated material relative to the field; this also deserves brief acknowledgement.
L362–385: The comparisons with previous ERW studies are thorough but scattered through the text. A synthesis table listing study, feedstock, application rate, system and the direction of response per gas would make the recurring "context-dependent" conclusion more systematic, and would enhance the impact of this research and be a valuable resource for readers.
L410–411: Lighting conditions are currently stated only in the Discussion. Please also specify in the Methods that measurements were conducted in darkness, so that readers have this information from the outset, since light affects CO and VOC photoproduction.
Conclusions:
L462–466: Since the soils were field-treated but measured only after air-drying, sieving, repacking and rewetting, the reported fluxes represent legacy effects of the field ERW treatment expressed under artificial laboratory conditions, rather than in-situ ERW responses. It would help readers if this were also mentioned in the Abstract, with the Conclusions worded slightly more cautiously. Relatedly, the measured fluxes should not be read directly as the trace gas footprint of real-world ERW deployment. Could the authors comment on the likely direction of bias relative to field conditions, for example, whether the absence of plants and roots, the disturbance of soil structure by sieving, and the constant laboratory conditions would tend to over- or underestimate particular fluxes, or bias different gases in different directions?
I hope the authors find these comments helpful, and I look forward to reading the revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-4380-RC2 -
RC3: 'Comment on egusphere-2026-4380', Anonymous Referee #3, 09 Sep 2026
reply
Summary
This paper presents laboratory incubation experiments on soils collected from field trials of enhanced rock weathering (ERW) across different land uses in the UK. Over a one-month incubation period, various soil gas fluxes were measured relative to a control treatment. The paper is generally well written, presents interesting data, and could contribute to constraining greenhouse gas balances associated with ERW deployment. However, I have several general comments that should be addressed before publication.
General comments
Relevance of measured fluxes to net carbon dioxide removal: The measured fluxes are never placed in context relative to the expected CO₂ removal from enhanced rock weathering. I appreciate that a full carbon balance may be beyond the scope of this study, but at minimum the authors should discuss whether the observed fluxes are negligible, comparable to, or larger than the anticipated removal rates. This context is essential for readers assessing the practical implications of the work.
Process-level interpretation of pH effects: The hypothesis that gas fluxes respond to basalt-induced increases in soil pH is central to the study, yet the discussion offers little mechanistic insight into how the measured fluxes relate to the proposed processes. For example, pH-driven desorption of soil organic matter could increase substrate availability and hence microbial activity, which in turn could affect gas fluxes. I encourage the authors to connect their observations more explicitly to these mechanisms, supported where possible by their own ancillary data.
Clarity and correctness of Equations 1–3: I struggled to follow the application of Equations 1–3. In their current form, the units on the left- and right-hand sides do not match, which suggests either errors in presentation or, more concerningly, in the underlying calculations. I can only hope the former. Please define every term and its units and verify dimensional consistency throughout.
Influence of measurement technique: Three different chamber approaches (dynamic, closed, and static) were used across the experiments. The paper does not assess how these methodological differences affect flux estimates or inter-experiment comparability. Are the resulting fluxes directly comparable?
Citation: https://doi.org/10.5194/egusphere-2026-4380-RC3
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The study presents measurements of nitric oxide (NO), ammonia (NH3), carbon monoxide (CO), hydrogen (H2), volatile organic compounds (VOCs), CO2, methane (CH4), and nitrous oxide (N2O) from control and ERW-treated soils collected from arable, grassland, broadleaf forest, and conifer forest field trials in the UK. Overall, the effects of ERW on trace gas fluxes varied among gases and soil types, with no consistent response across all sites. Significant treatment effects included lower CO2 emissions in both forest soils, greater CH4 uptake in broadleaf forest soil, higher NO emissions in grassland soil, and changes in CO and hydrocarbon fluxes in forest soils. NH3 and H2 showed no significant treatment effects, and no individual VOC remained significant after correction for multiple testing.
I enjoyed reading the manuscript. One of its main strengths is the broad range of gases considered, beyond the greenhouse gases that are more commonly measured in ERW studies. The results also show that trace gas responses to ERW can be quite variable among land uses and gas species. I agree with the authors that longer-term field measurements, together with more detailed soil and microbial characterization, will be important for understanding how these responses develop as the applied material continues to weather. The authors also acknowledge several important limitations, including the snapshot nature of the measurements and differences among sites in application history and trial duration. I have the following comments that I hope will help improve the manuscript.
Line 106–107: Please clarify why soil subsamples from the three field subplots were pooled into a single composite sample for each treatment. The same issue also applies to the grassland and forest soils. Once the field replicates are pooled, the subsequently prepared laboratory chambers are subsamples of the same composite sample rather than independent field replicates. How was this accounted for in the statistical analysis? It would also be helpful to clarify whether the treatment comparisons should be interpreted as comparisons between composite samples rather than replicated field-level treatment effects.
Line 243–244: Please check the definition of the boxplot whiskers, also in the other figure captions. The caption states that the whiskers extend by one interquartile range (IQR) from Q1 or Q3, whereas the conventional Tukey boxplot uses 1.5 × IQR. Please confirm which definition was actually used in the plotting code and revise the caption if needed.
Line 307–308: I am not sure that “hydrocarbon uptake was greater under ERW, particularly in conifer soils (p < 0.05)” is consistent with Table S3. For conifer soil, the significant difference appears to be in net hydrocarbon flux (p = 0.014), while the uptake component itself is not significant (p = 0.211). Should “uptake” be replaced by “net flux” here? The following statement on higher hydrocarbon emissions in broadleaf control soils is supported by Table S3 (p = 0.028), although both treatments show net hydrocarbon uptake in Figure 5.
Line 441–442: Please check the statement that naphthalene emission increased with increasing soil pH. ERW increased soil pH, but naphthalene emissions were lower in the ERW-treated forest soils. If higher pH reduces naphthalene sorption, one would instead expect this to increase its potential emission. I suspect that “increasing emission” may need to be “decreasing emission.” This would also be consistent with the explanation given in the next sentence, where increased microbial degradation at higher pH is suggested as a reason for lower naphthalene emissions.
Line 454–457: The two explanations proposed for the lower monoterpene emissions under ERW could be explained more clearly. Litter decomposition is itself largely mediated by microorganisms, so a decrease in litter decomposition with increasing pH may seem inconsistent with the next suggestion that increasing pH enhances microbial activity and monoterpene metabolism. These two mechanisms may involve different microbial groups or processes, but that distinction is not clear as currently written. Please clarify how these two explanations could operate, or provide additional support for them.