the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 29 Jul 2026
Evidence of microbially accelerated weathering from a laboratory mesocosm experiment with sequential selective dissolution
Abstract. Microbially accelerated weathering (MAW) is a promising soil-based carbon dioxide removal (CDR) strategy that leverages beneficial soil microbes to increase weathering of preexisting silicate minerals. This approach does not require addition of a mineral feedstock, greatly reducing the carbon footprint from mining, grinding, transporting, and applying the mineral to land compared with enhanced weathering. A key obstacle to measurement, reporting, and verification for MAW is ensuring that increases in weathering products, such as base cations, are sourced from silicate dissolution rather than redistribution of pre-existing cations from the exchangeable, oxidizable, or reducible soil pools. To address this, we conducted a 63-day mesocosm study with soybean, utilizing soil sequential extractions to track the buildup and distribution of weathering products in soil columns inoculated with Bacillus subtilis strain MP1. Our results indicated that MP1-treated soils yield a net increase in available base cations, corresponding to a 4.5 % increase in base cation charge relative to control soils. The observed increase in base cations is partitioned between the carbonate and exchangeable soil pools. We estimate that 37 % to 67 % of the weathering derived base cations formed carbonates, corresponding to a CDR of 0.20 to 0.36 g CO2 kg-1 soil. These findings suggest that Bacillus subtilis MP1 couples silicate mineral dissolution with carbonate precipitation, providing support for MAW as a viable and scalable CDR strategy.
Status: open (until 09 Sep 2026)
- RC1: 'Comment on egusphere-2026-4145', Anonymous Referee #1, 30 Jul 2026 reply
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CC1: 'Author Comment on egusphere-2026-4145: Supplemental Tables and Figures', Corey Lawrence, 05 Aug 2026
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Please find the supplemental figures and tables for egusphere-2026-4145 attached. They were inadvertently omitted from the preprint file.
Sincerely,
Corey Lawrence-
RC2: 'Reply on CC1', Susana Ferreira, 06 Aug 2026
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Thank you for providing the supplementary figures and tables that were missing from the original preprint. The additional material is clear and helpful for supporting the study. I appreciate the update and look forward to the revised manuscript addressing the reviewer comments.
Citation: https://doi.org/10.5194/egusphere-2026-4145-RC2
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RC2: 'Reply on CC1', Susana Ferreira, 06 Aug 2026
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RC3: 'Comment on egusphere-2026-4145', Anonymous Referee #2, 24 Aug 2026
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General comments
This manuscript describes a study intended to demonstrate the effect of a microbial inoculation of soya seeds on the ability of a soil-plant system to remove atmospheric CO2. The authors found statistically significant increases in soil inorganic carbon content, but weak or no differences in compositions of leachates collected from the pots. If correct, these findings show that natural soils are able to increase the rate of pedogenic carbonate formation as a consequence of inoculation with selected bacteria. This finding is well-known from work on microbially-induced carbonate precipitation, a technique used by geotechnical engineers to stabilise soils. They achieve this by adding a calcium salt to inoculated soils.
Specific comments
This study demonstrates the importance of understanding both accuracy and precision, especially when using commercial laboratories. I’ll explain the weaknesses below.
When compositional differences are slight, as in this study, it is really important to know what the analytical precision is for the experimental work, as sometimes the error bars on the lab analysis are greater than what is seen statistically as variability between replicates, if the numbers are taken at face value. This is especially true when external laboratories are used. They will usually quote precision under ideal conditions; the labs have to be tested by submitting a single sample split to give 4 or 5 ‘unknowns’, carefully each given a unique label, so the researchers can then calculate the precision that applies (for all analytes) for their specific study. That hasn’t been done in this case, so it is difficult to know if the statistical analysis that has been carried out can be trusted.
Regarding accuracy, the analysis of the soil demonstrates some of the problems that simply taking the numbers as true can present. There is no way that a soil with 65% quartz and 28% feldspars (XRD) can have the chemical composition reported by XRF. So the XRD and XRF analyses differ in their accuracy. Taking into account the ignition loss, I recalculated the composition using the XRD results and obtained: 72.4% SiO2, 6.8% Al2O3, 0.5% CaO, 1.6% Na2O and 1.1% K2O. In any case, at 15%, the reported LoI is really (suspiciously?) high for a sample with 2.6% organic C and a total maximum clay content of 5% phyllosilicates (the only hydrated minerals). We don’t know how to account for that very high value for LoI, so there is an additionally inaccuracy somewhere in the numbers.
Because of these observations, something has evidently gone wrong right at the start. At best, maybe two different samples have got muddled by the labs. But it is more likely one set of numbers is wrong (I would suspect the XRD). This needs to be sorted out, as associated errors affect the interpretation of the data, especially as the sequential extraction and TIC results need to obtain Ca from somewhere.
A problem also affects the determination of organic C by difference. Here there is a propagation of analytical error, as the combustion-based determination of total carbon has an analytical precision that needs to be added to the precision of the inorganic carbon determination to estimate the precision of the calculated value for organic carbon. It is a pity that the organic C content was not determined directly by combustion – something that is easily done using thermal analysis or an instrument such as the LECO RC612. Given that a single soil is used for all the columns, it would be worth thorough analysis of its carbon content through direct determination using these techniques.
The description of the method is given in detail, and so other workers would be able to reproduce the experiment. However, it is stated that the seeds were inoculated with 1 ml of water. That is greatly in excess of the size of the seed, and so I wonder if they were inoculated with 1 microlitre of water – which would then enable the statement in line 99 to make sense.
Charge balance has been assessed for the leachate analyses. The calculated charge balance should be made known to the reader. It is acceptable to assume that a positive surplus might be counterbalanced by bicarbonate, but how does that calculated value compare with the measured values? In my experience, charge imbalance often arises from error in the determination of anions.
So, overall, I think there are issues regarding the experimental data that need to be resolved before we can judge the validity of the statistical interpretation of the results. The interpretation of the base cation data for the carbonate step of the extraction should also be reconsidered, as there is no reason why K or Na should be associated with dissolution of a carbonate mineral – K and Na carbonates are unlikely to be present in a natural soil.
I recommend a second round of review after the analytical data have been properly audited, verified and interrogated prior to statistical analysis.
Technical corrections/typos
Line 124: the x in X-ray should be upper case.
Line 126: soil organic matter determination by combustion at 360°C is a very rough estimate – some hydrated minerals report, and refractory forms of soil carbon, very much part of SOM, are stable up to higher temperatures and so don’t report.
Line 151 and elsewhere: use proper IUPAC formulae (or write the chemical name in full) rather than using the informal ‘Ac’ to denote acetate – it could mean something quite different.
Line 164: which yttrium salt was used? It might well not be metallic yttrium.
Line 172: ‘equal masses’ would be better.
Line 183: say which section the description is in – it isn’t in the ‘previous section’.
Line 202: explain what you mean by ‘volume weighted pH’. pH is an intensive parameter, and so is independent of sample volume.
Line 257: please provide more information concerning the K (and Na) data, as the values are too small to read from the graphs. The same goes for Al in Figure 5.
Line 440: Would ‘In contrast’ be better than ‘Whereas’?
Citation: https://doi.org/10.5194/egusphere-2026-4145-RC3 -
RC4: 'Comment on egusphere-2026-4145', Anonymous Referee #3, 25 Aug 2026
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Lawrence et al. present results of a 63 day mesocosm experiment testing whether inoculation with a microbial strain, B subtilis, increases silicate weathering, and resulting carbon dioxide removal, in an agricultural soil. The authors use sequential selective extractions to trace how potential weathering products are distributed amongst different soil, plant, and leachate pools. I found the study interesting and relevant for SOIL readership. However, I share some of the concerns of the other reviewers regarding the characterization of the soil used in the experiment, the lack of baseline sequential extraction measurements, the statistical treatment of the data, and the strength of some of the conclusions drawn from the study. I believe that major revisions are necessary before the study could be published in SOIL.
Major Comments:
1. Soil characterization
I agree with Reviewer 2 that the mineralogical and elemental characterization of the soil needs to be clarified. The results do not seem to match particularly well, given the very high proportion of quartz and feldspar reported. Because the interpretation of the experiment depends on silicate minerals being the source of the additional base cations, I think this discrepancy should be explained more clearly. I was also surprised by the 15% LOI. The measurement at 360 C is useful for an operational estimate but not equivalent to a high temp LOI. Given the reported ~2.6% SOC and only 5% phyllosilicates, 15% mass loss seems unexpectedly high. As some of the reported treatment effects are relatively small, it would be helpful to see some more information on the analytical uncertainty, particularly detection limits and measurement precision.
2. Experimental baseline and control treatment
I agree with Reviewer 1 that the lack of baseline sequential extraction measurements complicates the interpretation of the results a bit since there is no direct measurment of how the cation pools changed relative to initial conditions. What was the rationale behind no baseline extraction? Perhaps it is also worth discussing the lack of a control with no soybean plant? While the experiment can isolate the additional effect of MP1 in the presence of soybean, it cannot separate background/abiotic weathering from plant/rhizosphere driven weathering. I think these limitations should be acknowledged more clearly, particularly when discussing the sources of cations and the responsible mechanisms for the observed treatment effects.
3. Statistical analysis
I agree with Reviewer 1 that the statisical analysis could better reflect the experimental design. At the moment, many of the depth-specific results are tested separately, even though the three depth intervals come from the same mesocosm and are therefore not independent. A treatment x depth analysis or mixed effects model with mesocosm included as a random effect seems more appropriate. Additionally, the methods state that either a student's t-test or Mann-Whitney U/Wilcoxon rank-sum tests were used, while the captions for Figures 1 and 3 report Wilcoxon signed-rank tests. Were the UTC and MP1 columns paired in some way? If so, please describe the pairing in the experimental design; if not, please clarify which statistical test was used. There are also a large number of separate tests across depths, elements, and extraction fractions, so it would be helpful to clarify whether multiple testing was considered.
Minor comments:
L26-L65: The introduction is generally well referenced, but a few of the broad claims could use citations, particularly those regarding agricultural co-benefits, preference of EW for acidic soils, and CDR consequences of carbonate precipitation.
L65-70: "definitively link" seems too strong given limitations of study. I would also consider changing "all potential sinks" to "major measured sinks"
L75: "microbial amended" -> "microbially amended"
L98-100: Please check the inoculation-rate calculation. The manuscript states that 3.9 x 106 spores were added per mesocosm and that this correspons to 3.9 x 103 spores/g soil but this does not seem consistent with either the wet or dry soil mass.
L215–225: I would state more clearly here that the SIC/TIC treatment difference was not statistically significant. The text currently emphasizes the ~37% increase, whereas the following section notes that TIC was near the detection limit and not significant.
L350–360: The discussion of depth-dependent rhizosphere activity and pCO2 is interesting, but neither root abundance nor pCO2 was measured. I would make it clearer that this is a proposed explanation.
Citation: https://doi.org/10.5194/egusphere-2026-4145-RC4 -
RC5: 'Comment on egusphere-2026-4145', Anonymous Referee #4, 26 Aug 2026
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This manuscript presents biogeochemical evidence for microbially accelerated weathering and provides valuable data for improving measurement, reporting, and verification of carbon dioxide removal (CDR). However, several key conclusions appear to extend beyond the direct evidence provided by the dataset. The differences in pH, DIC, SIC, TIC, and exchangeable base cations between the control and microbially treated soils were not statistically significant overall, although some differences appeared at specific soil depths. Given the inherently slow timescale of silicate weathering, the relatively small magnitude of the observed changes raises the question of whether the incubation conditions (e.g., temperature and duration) were sufficient to detect measurable differences in CDR within the timeframe of the laboratory experiment. In addition, the basis used to compare the control and treatment should be clarified. For example, it would be helpful to specify whether the reported concentrations were normalized by dry soil mass, soil bulk density, or extract volume. These issues should be addressed before the conclusions regarding CDR can be robustly supported.
Citation: https://doi.org/10.5194/egusphere-2026-4145-RC5
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I enjoyed reading this manuscript. It addresses an important question for microbially accelerated weathering and presents a well-designed mesocosm experiment. The manuscript is clearly written, the methods are well described, and the discussion is generally balanced. I particularly appreciated the use of sequential selective extraction together with a mass-balance approach to strengthen the interpretation of weathering products.
Overall, I think this is a solid study that is suitable for publication after minor revisions.
Main comments
Minor comments