This is an interesting experimental study on the effect of ERW using basalt, especially since it employed macrocosms that were monitored over time. This enabled the authors to determine the inorganic and organic budgets directly from the measurements, as opposed to modelling. It is also interesting that you found a significant CO₂ intake leading to the same extent of C storage.

comment#1:  My main comments concern the discussion section, which I found to be very poor. Firstly, you dismissed the possibility of carbonate precipitation being responsible for C storage after ERW (due to the lack of an increase in dissolved inorganic carbon). See 4.2. Why should carbonate genesis occur at the surface? The localisation of carbonate precipitation depends on the ratio between the precipitation rate and the mass transport rate. How can carbonate precipitation in June–July explain C storage in August and September? I think there has been carbonate precipitation since the beginning, certainly driven by relatively high temperatures and dry conditions. However, you cannot prove this due to the lack of chemical data (e.g. Ca, Mg) and geochemical modelling.

We would like to clarify that we did not intend to dismiss the possibility of carbonate precipitation. Rather, we stated that our dataset provides no direct evidence for it, while acknowledging that our experimental design may not have been suited to detect it. For instance, carbonate formation could have occurred below 20 cm depth, as the reviewer correctly points out; but this message is indeed poorly convened in the discussion. Concerning the second part of the comment, our point was that carbonate formation rates may simply have been below the detection limit of our sampling strategy. Even small concentration changes over a three-week interval—the frequency of our sampling—could translate into significant cumulative storage at the macrocosm scale over an entire growing season. In addition, the number of samples collected during the driest period was limited, which could also explain why carbonate formation was not captured. In this sense, we are in agreement with the reviewer’s interpretation, though we acknowledge that our original discussion did not convey this clearly. We will revise Sections 4.2 and 4.3 to better reflect this:

Replace

"Nevertheless, two plausible explanations remain for why bicarbonates might have gone undetected: first, potential sub-surface bicarbonate formation beyond our 20 cm measurement

depth, although carbonate genesis typically initiates closer to the surface; second, extremely gradual topsoil carbonate 390 formation rates, particularly during the dry June–July period when most soil water was unavailable for sampling. While our current data provide no support for ERW-mediated reactions, we acknowledge methodological limitations prevent definitive

conclusions regarding their occurrence."

by

"Nevertheless, three plausible explanations remain for why bicarbonates might have gone undetected: first, carbonate genesis occurs at the surface only if precipitation outpaces mass transport. If mass transport is faster than precipitation, carbonate can form deeper rather than being confined to the top 20cm, where we took our samples from; second, even small concentration changes over a three-week interval—the frequency of our sampling—could translate into significant cumulative storage at the macrocosm scale over an entire growing season; third, the number of samples collected during the driest period was limited, which could also explain why carbonate formation was not captured. Hence, while our current data provide no direct support for ERW-mediated reactions, we acknowledge methodological limitations prevent definitive conclusions regarding their occurrence."

comment #2: Secondly, although microbial activity is the only consistent variation, and roots are severely depleted after ERW, you emphasised the role of root exudates in explaining the increase in C storage as organic C in section 4.3. What about the increase in microbial biomass and dead cells? Wouldn't increase in microbial activity be likely to increase exudate degradation and thereby CO₂ emission? [...] However, I am not convinced that LMWOAs are preferentially released to enhance microbial activity, as it is insensitive. Nevertheless, I meant that more microbes may be related to more dead cells, which, along with secondary minerals, are an important factor in stabilising organic carbon (hence more CO₂ intake by the soil?).

We suggest to add the following paragraph at the end of the discussion:

"The two preceding explanations appear unlikely, as they are insufficient to account for the observed large increase in carbon sequestration. An alternative to enhanced root exudation is that the basalt treatment stimulated microbial biomass production. This stimulation could initially cause additional CO₂ emissions from the soil but, after microbial death, lead to substantial incorporation of metabolized carbon into associations with soil minerals. Such “microbial entombment” is known to produce highly recalcitrant carbon forms (Xiao et al., 2023). This interpretation is also consistent with our observation of increased microbial activity under the basalt treatment. If microbial turnover is particularly rapid, this mechanism could explain the significant carbon sequestration measured in our experiment and would be especially noteworthy, as it suggests that microbial entombment may represent a carbon storage pathway for enhanced rock weathering (ERW) comparable in importance to carbonate formation."

comment#3: You state in the abstract that C storage is beyond the effect of electrochemical transformation (I assume you mean Ammann et al., 2022), but I cannot find any convincing demonstration of this in the main text.

This is very likely a vocabulary mistake from our side, we mean “weathering rate” instead of electrochemical transformation. We will then correct lines 374-377: " Remarkably, this figure slightly exceeds the theoretically achievable limit of converting applied basalt into entirely carbonates (144 kg/ha for a 10 t/ha amendment). Hence, either complete transformation of the amendment occurred exceptionally swiftly within three months, which appears improbable based on existing literature (Kelland et al., 2020), or alternative mechanisms contributing to soil carbon sequestration must be considered.”

We also suggest to replace

"Furthermore, the magnitude of carbon sequestration exceeded what could  solely be attributed to electrochemical transformation."

by

"Furthermore, the magnitude of carbon sequestration exceeded what could  solely be attributed to weathering rates."

comment #4: I think all the equations should be numbered, and all the units should be given.

We will number the 4 equations in the Material & Methods section and provide units for each;

comment #5: Why should basalt at the surface lead to greater soil disturbance (and corresponding CO₂ emission)?

You are probably referring to the sentence: “Immediately after applying basalt, elevated CO₂ emissions occurred likely due to soil disturbance (Figure 2).” We understand your point that since all plots were tilled during seeding, and basalt was applied at that time, there is no obvious reason why the basalt-amended plots should have experienced greater disturbance and CO₂ release. This is a valid observation. We think that the presence of basalt may have stimulated microbial activity, leading to higher CO₂ emissions a few days after application. We propose to revise this discussion point accordingly, if you agree with this interpretation. We therefore replaced (in the results section)

"Immediately after applying basalt, elevated CO₂ emissions occurred likely due to soil disturbance (Figure 2)."

by

"A peak of CO₂ emissions occurred immediately after soil disturbance (tillage for seeding), and this peak was larger under basalt treatment (Figure 2)."

And in the discussion section we suggest to add the following sentence:

“Because all plots were tilled during seeding and basalt was applied at that stage, there is no clear reason why the basalt-amended plots should have undergone greater disturbance or CO₂ release. We propose instead that the presence of basalt may have stimulated microbial activity, resulting in elevated CO₂ emissions a few days after application in the treated plots.”

Comment#6: I also have plenty of minor comments, and these are only a few of them. I will give you the rest if they persist in the second round.

Table S1 : which mineral is 2:1 Al clay?

We understand this to refer to layer silicates with an Al-dominated octahedral sheet. This describes a group of minerals with a characteristic structure, rather than a single specific mineral.

Comment#7: Table S2 : special character editing issue in the headings

Will be corrected

Comment#8: Figure S6 : what are the R-squared and the number of samples? Typo: "top" instead of "sop"? p-value = 3.8.10-9

Will be corrected

Comment#9: One minor comment: it looks like there is a missing read character in Figure 1. Can you see all the fluxes other than plants and soils?

Indeed, the basalt treatment should appear in red for all fluxes, which was not the case. This will be corrected.

Please note that the comments are numbered in common for all the reviewers.

In their manuscript “Enhanced weathering leads to substantial C accrual on crop macrocosms” the authors present a mesocosm experiment (called “ecotron”) on  carbon sequestration in soil cores upon application of finely ground basalt (<1mm). The soil cores were chosen and prepared to mimic the conversion of marginal lands to agricultural lands. The experiment was carefully set up. We particularly appreciate the measurement of all three major greenhouse gases (CO₂, CH₄, and N₂O). The full control of the atmospheric gas composition in the ecotron facility makes it possible to achieve a full carbon mass balance of the system. The inclusion of uncertainty and sensitivity analyses on plant roots and dissolved inorganic carbon (DIC) leaching via bootstrapping adds robustness to the results. In addition, the discussion around the potential stabilization of root exudates by weathering products and the subsequent formation of mineral-associated organic matter (MAOM) is valuable.  The manuscript is well structured overall; we have a few suggestions for restructuring the text to enhance the story line. But several sections should be strengthened before publication. For example, the introduction section is very short and contains sloppy wording on core concepts (see detailed comments below). The discussion section lacks detail on the potential changes in plant metabolism that could explain observations. This study definitely merits publication but the comments below need careful consideration.

Comment#10: Bring introduction section in line with state of the art: The introduction section does not capture the state of the art of ERW research For instance, the absence of DIC leaching to deeper water layers, the complications introduced by interactions between the organic and inorganic carbon dynamics in natural soils (e.g. impact of weathering on SOM stabilization, soil organic carbon decomposition and plant C inputs), the difficult to quantify role of secondary mineral formation (PIC, clays, Fe/Al (hydr)oxides) are all well established and merit consideration. In this sense it lacks some recent references (e.g. Vicca et al (2022) Vienne et al. (2024), Steinwidder et al. (2025), …). A more complete and up to date description of the state of the art will strengthen the introduction, with as additional benefit to further support the relevance of the underlying study.

We thank the reviewer for this useful suggestion. We suggest to add the following text in the introduction: “Assessing the net impact of enhanced silicate weathering on soil carbon budgets is for example complicated by the tight coupling between organic and inorganic carbon dynamics. On the one hand, silicate dissolution contributes to inorganic C sequestration through carbonate precipitation and organo-mineral associations, such as stimulation of mineral -associated organic matter (Xu et al., 2024). On the other, it indirectly influences the largest terrestrial C pool—soil organic carbon—via changes in nutrient availability, microbial activity, litter quality, and aggregate formation. These processes can either promote stabilization of organic matter or accelerate its mineralization, with outcomes that vary across timescales and soil types (Vicca et al., 2022). In addition, secondary mineral formation (e.g. clays, Fe/Al (hydr)oxides, or pedogenic carbonates) can reduce DIC availability for export while providing new sorption surfaces that affect SOC stabilization. While enhanced weathering is typically framed in terms of inorganic CO₂ sequestration through pedogenic carbonate formation or leaching of dissolved weathering products, these fluxes can be relatively minor compared to other soil C processes. A substantial fraction of released base cations may instead be retained on exchange sites or incorporated into secondary minerals such as clays or Fe/Al (hydr)oxides, thereby bypassing direct CO₂ uptake. Moreover, organic carbon fluxes often exceed inorganic fluxes by orders of magnitude, with soil organic matter decomposition potentially releasing far more CO₂ than is sequestered via mineral weathering. At the same time, silicate amendments can enhance plant productivity and promote the transfer of organic C into more stable soil fractions through aggregation and mineral associations (Vienne et al., 2024). These contrasting effects illustrate the difficulty of isolating a single mechanism and highlight the need for integrative approaches that jointly consider inorganic sinks, organic matter dynamics, and secondary mineral formation when evaluating the true CO₂ removal potential of enhanced weathering (Steinwidder et al., 2025). Together, these processes illustrate that reliable estimates of carbon dioxide removal (CDR) through enhanced weathering must account for both inorganic and organic C pools, as well as the role of secondary mineral phases, rather than focusing solely on weathering rates.”

Comment#11: Context of marginal land application: It should be stressed that basalt was applied on artificially marginalized land that has been subjected to fertilization and cropping in the mesocosm setup. This is crucial to contextualize the results, as the implications may differ from intensively managed agricultural systems. Positioning the work in this context, in line with and related literature (e.g. https://doi.org/10.3389/fclim.2022.928403), could highlight the potential of enhanced weathering (EW) to increase food production and carbon sequestration on marginal soils, particularly in the Global South.

Indeed, it’s an interesting point. This work doesn’t support the hypothesis that EW can improve food production, though, as crop yield was not affected in our results. However we agree that the increase in soil TOC is potentially relevant for soil health in general. We suggest to add the following text in the introduction:

“To address these limitations, we conducted an EW amendment experiment on an artificially marginalized land that has been subjected to fertilization and cropping, within an ecotron—a controlled, closed-environment facility that enables real-time monitoring of ecosystem-level carbon fluxes (Roy et al., 2021).”

And in the discussion:

“This is especially significant given that our experimental macrocosms were established on marginal soils, where increases in SOC are typically associated with improvements in soil health, such as reduced erosion, enhanced water retention, and greater nutrient storage capacity. These results confirm that enhanced weathering—a potentially low-cost strategy—could strengthen both carbon sequestration and soil health on marginal lands (Ivan A Janssens et al., 2022), particularly in the Global South.

Comment#12: Discuss importance of biological processes: The comprehensive mass balance results show that increases in soil carbon are the primary driver of carbon sequestration. However, the manuscript does not fully articulate the logical implication that this increase is likely due to enhanced CO₂ uptake through photosynthesis, followed by subsequent release as root exudates (that can be stabilized in MAOM) (see e.g. https://www.science.org/doi/10.1126/sciadv.abd3176). In our opinion the discussion should be elaborated, and emphasize that biological processes, rather than geochemical mechanisms (DIC + PIC increases), appear to be the dominant contributors to the observed CO₂ uptake. Specifically, the fertilization effect of basalt (enhanced nutrient availability) in driving the observed changes in net ecosystem exchange (NEE) and CO₂ fluxes after basalt addition deserves stronger emphasis.

We respectfully disagree with that comment. We actually dedicate a full discussion section to address the potential role of biological processes in the observed sequestration (section 4.3). We also don’t think that we can conclude to any fertilization effect of basalt as we found no significant difference in plant biomass in the two treatments. However we agree that we did not completely articulate that increase in root exudates or microbial activity would be initiated by enhanced plant photosynthesis. We therefore suggest to add the following text in the discussion:

“Although root exudates alone are unlikely to fully account for the magnitude of carbon storage observed, their role in MAOM formation represents a significant component of the coupled organic–inorganic processes underlying ERW-driven sequestration. An alternative explanation is that basalt treatment indirectly stimulated microbial biomass production, through a combination of increased root exudation and improvements in soil physical and biochemical conditions. This stimulation could initially lead to additional soil CO₂ emissions, which aligns with the patterns observed in our experiment;”

Comment#13: Incomplete characterization of t0 : Methodologically, the characterization of t0 is confusing. In our opinion, the experiment starts at the beginning of the basalt amendment. However, soil pH and soil organic carbon are given at the time the soil cores were taken from the field. Between this time and the actual start of the experiment, the mesocosms were subjected to cropping and fertilization. Concerning the soil characteristics after the transition period, the authors only briefly mention that “the pH was 7 in all units”. This is a high and atypical value for agricultural soil, and no information on vertical variation in pH is provided. No mention of soil carbon at the start of the experiment is given. It would strongly strengthen this paper if soil pH and organic carbon were available at t0 of the experiment. This is particularly relevant when interpreting the experimental results in terms of real agricultural systems. Including pH data after application would further strengthen the dataset and provide valuable context regarding soil chemistry changes.  If soil samples were taken at the end of the experiment and are still present, this could be an interesting addition to the dataset.

Unfortunately the soil samples taken at the beginning of the experiment have been used for other purposes and we cannot run these measurements again. We would just like to clarify that soil pH was neutral at the beginning of the experiment as we used 10 t/ha equivalent of CaCO3 to correct for soil acidity at the beginning of the previous growing season. We will add this information in the M&M.

Comment#14: We further have the following detailed comments and suggestions: 

Abstract:

Mention that you monitored all GHGs in deep mesocosms and emphasize that 10 ton basalt ha-1 was added to degraded soils first. Emphasize that this experiment was not done on a typical rich agricultural soil.

We will correct as follows: “We monitored all greenhouse gases in deep mesocosms representative of marginal soil conditions and applied 10 t ha⁻¹ of basalt at the start of the experiment.”

Comment#15: L30  “It involves the application of silicate rock powder to soils, where it is expected to react with CO₂ released from soil respiration, forming stable carbonate Ions". While this is an intuitive way of understanding the weathering process, it is more correct to rephrase it along the lines “Dissolution of silicate minerals enhances the alkalinity of the pore water, resulting at a shift of the carbonate system towards carbonate and bicarbonate, leading to higher dissolved inorganic carbon when the water is equilibrated with the atmosphere”.

We will correct accordingly.

Comment#16: L33: 1.5 tons ha-1 sequestration; please specify that this is ton C ha-1 and not ton CO2 ha-1. Also add the timescale after which this C sequestration took place, 150 days = 1 growing season I suppose? 

We specify in the same sentence that we refer to “measured carbon flux into the soil”, hence we think it is already clear that the results are expressed in ton C ha-1 and not ton CO2 ha-1. We will add that the results were obtained during one growing season.

Comment#17. Change electrochemical transformations into “geochemical C sequestration” or specify that DIC or PIC increases could not explain the observed C sequestration. Throughout the MS: change electrochemical into geochemical.

We will correct accordingly.

Intro:

Comment#18: L39 – The first sentence does not make sense. The relative contribution of agriculture to GHG emissions, does not “highlight the urgent need for scalable mitigation strategies.” If the authors want to stress the urgent need for mitigation, they can support and strengthen that argument with recent reports and publications on risks involved with the current emission pathways, literature on tipping points, etc ... 

We will delete this sentence.

Comment#19: L41 Please be more specific. ERW should not be framed as a major mitigation strategy, but as a negative emission technology and a CDR method, specifically proposed to achieve a net negative GHG balance in the near future.

We will correct this sentence accordingly: “Enhanced rock weathering (EW) has emerged as a promising negative emissions strategy and carbon dioxide removal (CDR) approach, specifically aimed at achieving a net negative greenhouse gas balance in the near future and reducing carbon emissions from the agricultural sector”

Comment#20: L42 “where it reacts with CO2 etc...” -> see comment on abstract. Please rephrase accordingly. 

We will rephrase the sentence as follows: “The method involves applying silicate rock dust to soils, where the dissolution of silicate minerals increases the alkalinity of pore water, shifting the carbonate system toward carbonate and bicarbonate ions and leading to higher dissolved inorganic carbon when the water equilibrates with the atmosphere.”.

Comment#21: L42 – L50 This core part of the introduction section does not capture the state of the art of ERW research. (see general remark)

See reply to comment#10.

Comment#22: As mentioned above, the authors should introduce and motivate the relevance of specifically studying  ERW on marginal soils that are converted to agriculture and clearly mention the artificial “marginalization” and conversion in the mesocosm setting.

See first part of the reply to comment#11 for what concerns the introduction.

Methods:

Comment#23: 2.1 Ecotron facility

Remove “(as Heading 1)” in the section title

Thanks for spotting this. We will correct accordingly.

Comment#24: L61 adapt to “[...] in gas-tight enclosure. High-frequency measurements allow [...]”

We will correct accordingly.

Comment#25: L62-L64 -> Move to introduction section

We will correct accordingly.

Comment#26: L62 “this enables to study the actual dynamics of the process of EW ...” this oversells the system bit. Please be more precise, e.g. along the following lines: “This enables us to close the carbon mass balance in the system and to study the fate of released cations, while the large mesocosms [...]”

We will correct accordingly.

Comment#27: Lacking from the “ecotron”-part of the methods section is the way CO2 is regulated in the mesocosm -> L126-127 can be moved here.

We will correct accordingly.

2.2 Macrocosm

Comment#28: L83 “Six large macrocosms” -> Six large soil cores. In our opinion, it becomes a macrocosm once those cores are incorporated in the full setup.

We will correct accordingly.

Comment#29: L90: Agricultural treatments to mimic the conversion of heathland to crop fields.  Please mention which treatments these were? Only the foliar Si, and NPK fertilization? Can you add details on how much NPK was applied?

We used NPK fertilization at the same level in all units and Si foliar spraying in three of them. We added 100 N 80P 120K, with NH₄NO₃, NH₄H₂PO₄ and KNO₃. We will mention it in the manuscript.

Comment#30: L92: How deep was the basalt plowed in? 

20cm. We will add this information in the manuscript.

Comment#31: L93: Is there a more detailed basalt particle size distribution than just <1 mm particle size? More specific information on the particle size and the specific surface area (e.g. BET surface area) would greatly benefit comparison to other experimental studies.

Unfortunately we couldn’t retrieve more information on the particle size distribution and the batch used in the experiment is now gone. 

2.3 Climate simulations

Comment#32: L101-106 Move to Ecotron section. The current section should focus on the climate scenarios that were simulated, and how.

We will correct accordingly.

Comment#33: L100-101 and L109-110 convey are identical in message – remove one of both. 

We will remove the first one.

2.4 Plant biomass

Comment#34: L115: How were roots exactly measured? How much cores/m2 … for the entire 1.5m depth?

We did not use soil cores. As written in that section, we sampled entire plants (shoots + roots, by gently pulling them out of the soil – note that we comment also on that in the discussion to explain that we may have left some roots in the soil and we tried to correct for it in the bootstrap analysis) and weighted each organ separately.

2.5 CO2-C net flux

Comment#35: L126-127 move to the Ecotron section of the methods.

See reply to comment#27.

Comment#36: L133 “Data gaps were filled using a moving average function (ALMA function from the TTR package in R)” Please be more precise on the gap filling. Perhaps data was (linearly?) interpolated before running the moving average filter? 

Indeed. We will clarify this sentence.

2.7 Rainwater C flux

Comment#37: L150: Rainwater C flux: DOC in rainwater was measured, is inorganic C in rain water negligible? Or what are typical values please mention why this is not measured. 

Indeed, we did not measure inorganic C in rainwater, because all of the volume was used for TOC/TN measurements. We will clarify like this in this section “Note that, since the entire sample volume was used for TOC/TN measurements, we could not measure the inorganic carbon input from rainwater. However, as the rainfall amounts were the same for each unit—following the same climate projections—this should not confound the results.”

Comment#38: Non-purgeable C or  DOC, how was this measured, device, precision …?

We will correct accordingly.

Results: 

Comment#39: L259: The largest input flux, by far, came from net CO2 exchange (366 to 457 gC/m2 depending on the treatment) ==> not clear which one is basalt and which one the control from the text, please rephrase. 

We will correct accordingly: “366 to 457 gC/m² in control and basalt treatments, respectively”

Comment#40: L261: Not clear: were there significant differences in CH4 and N2O emitted after basalt amendment. Please add details. 

We do not cover N20 in this paper as we focus on the C cycle. We just wanted to mention that the macrocosms were C sinks whatever the treatment, though the treatment had no significant impact on the methane balance of the system. We will clarify this in the text: “The crop system was a net CH₄ sink throughout the experiment, but the treatment had no effect on methane balance of the macrocosm.”

Comment#41: L264, Figure 1: add the amount of days the growing season lasted. Add red / black everywhere for basalt/control to improve interpretation of this figure. 

We will correct accordingly.

Comment#42: Figure 2: please add error bars for the cumulative NEE differences around the red and black line. 

The standard error is already added to the graph, it is just barely visible. We will clarify this in the text.

Comment#43: L320: Table 1: should be a figure for visual interpretation or just move to the supplement.

We are not sure about that – this paper has already been submitted to several journals and we found that reviewers were mostly critical on these soil water analyses, while it was presented as a supplementary figure. We would prefer to keep them as a table in the main text, because we think they are crucial to convey the message that there is lots of variability, and that the extent of the gaps might explain that we may have missed some carbonate peaks.

Comment#44: Colors are not explained. 

We will correct accordingly: "Orange cells: concentrations above 5mg/L; red cells: concentrations above 10mg/L."

Comment#44: L342: I think the evidence for microbial activity is a strong result and may be included in the main text, potentially as an alternative for Table 1. 

We will correct accordingly.

Discussion: 

Comment#45: see general remark about discussing role of photosynthesis, root exudates and MAOM.

See replies to comments#1, #2 and #12.

Comment#46: L374: You’re mentioning that the C sequestration is higher than the theoretically  achievable inroganic C sequestration. Based on the EW potential of the rock, we assume the Renforth (2019) formula was used to calculate this. If not already cited, please cite this work in the methods somewhere. 

Indeed. We will clarify this in the M&M section 2.1.

Comment#47: L363: Enhanced CO₂ levels are known to stimulate both weathering rates and CO₂ uptake via electrochemically-driven reactions (Amann et al., 2022). ==> change to geochemically.

We will correct accordingly.

Comment#48: L357: Alternatively, carbon sequestration rates nearing 2 tons per hectare were realized within a single year using equal amendment quantities (10 tons per hectare), though this involved utilizing a more chemically reactive substance—olivine—as opposed to basalt (Dietzen et al., 2019). 

==> We believe Dietzen et al. 2018, measured an increase in soil respiration in the incubation experiment (Effectiveness of enhanced mineral weathering as a carbon sequestration tool and alternative to agricultural lime: An incubation experiment). A “CDR potential” is estimated if all Mg of the exchangeable pool were to leach out as Mg and charge balance with HCO3-. I think this is the value you refer to with “C-sequestration”. Please nuance that no proof of inorganic C sequestration was found in the referenced Dietzen et al, 2018 study.

That is true indeed, I did not pay enough attention reading that paper, thanks for the suggestion. We will correct the sentence accordingly.   

Comment#48: L366: Secondly, we also measured significantly higher microbial activity in basalt-amended soils, mirroring findings by Li et al. (2020), who reported a 33% increase in microbial activity following enriched rock-dust applications. 

Please add some recent literature to emphasize this point. The simulation work of Klemme et al. (2022) also suggests increases in SOM decomposition after basalt amendment and pH increase. Steinwidder et al. (2025) also makes this point.  Mention that for C sequestration in Kelland et al. (2020), only inorganic C was considered and that the reported sequestration was a modelled value. 

L379: On the lack of substantial DIC / Ca / Mg leaching, others are finding similar results (e.g. Steinwidder et al. (2025), Vienne et al. (2024), Amann et al. (2020)).

We will correct accordingly. We will add these references in the discussion  to strengthen the points on increase in microbial activity, on comparison with reported sequestration in Kelland et al., 2020, and lack of ERW evidence in other papers. We will also modifiy the concluding remarks of this section accordingly (“Therefore, although our data provide no direct evidence for ERW-mediated reactions, methodological limitations prevent us from drawing definitive conclusions regarding their occurrence. At the same time, we cannot exclude the possibility that some carbon was sequestered through pathways other than carbonate formation.”).

Comment#49: It is possible that processes such as cation exchange produce protons and degas DIC, please comment on this as a possible mechanism for the non-observation of a DIC increase in leachates.   

In that case, we indeed would observe no DIC in the soil water samples, but wouldn’t it lead to soil CO2 emissions and substantially decrease the C sequestration?

Comment#50: L405: Also mention the work of Noah Sokol on MAOM and EW, there is at least 1 field study that discusses this.  Other relevant recent work: https://doi.org/10.1016/j.scitotenv.2025.180179.

We will add these references and some discussion point to section 4.3 in the discussion.

Please note that the comments are numbered in common for all reviewers.

This manuscript rigorously investigates the efficacy of enhanced weathering (EW) as a climate change mitigation strategy, with a focus on carbon (C) accrual in crop macrocosms under projected future climate conditions. A key strength is its employment of a large-scale ecotron facility (4.7 m³ macrocosms, 1.5 m deep soil), which overcomes inherent limitations of prior field (uncontrolled C fluxes) and mesocosm (shallow soil profiles) studies by enabling comprehensive quantification of ecosystem-level C fluxes. The study demonstrates that EW enhances soil C flux and promotes C sequestration exceeding levels attributable solely to electrochemical processes, via both carbonate precipitation and enhanced biogeochemical activities. These findings provide novel evidence that EW drives substantial C sequestration in agricultural systems while challenging the traditional paradigm that EW-dependent C sequestration relies primarily on carbonate formation, thereby advancing understanding of EW’s mechanisms and scalability and offering critical insights for developing degradation-specific soil C management strategies. Nevertheless, several points require clarification to improve the manuscript’s clarity, logical coherence, and academic impact.

Comment#51: Lines 33-34: Caution is warranted regarding the conclusion that “EW treatment resulted in an almost three-fold enhancement of measured carbon flux into the soil, achieving rates up to 1.5 tons per hectare”. As noted in the manuscript, basalt weathering does not increase soil inorganic carbon levels but may elevate soil CO₂ concentrations. This observation raises critical mechanistic and quantitative questions: following the documented influx of substantial CO₂ into the soil, does this gas primarily store in soil pores? Given that free CO₂ in soil pores is inherently unstable and susceptible to re-emission to the atmosphere, it is imperative to quantify the fraction of this CO₂ that can be stably/ long-term retained in the soil under EW conditions. This question could be addressed by comparing short-term and long-term differences in soil CO₂ levels under EW Such quantification is essential for accurately delineating the actual CO₂ sequestration efficiency of EW, as only stably retained carbon contributes to long-term climate mitigation value-distinguishing transient soil CO₂ accumulation from durable carbon sinks.

If we understand your comment correctly, you are suggesting that CO₂ may have been sequestered primarily as a gaseous pool, rather than in DIC, DOC, MAOM, POM, or particulate inorganic C. This is an interesting idea, but unfortunately we are unable to test it directly in our study, as the macrocosms were dismantled at the end of the experiment in 2023 and we do not have measurements of soil CO₂ concentrations. We would, however, like to note that the soil gaseous CO₂ pool is generally considered negligible compared with pools such as SOC or DOC, which are orders of magnitude larger. In addition, this pool is highly transient due to respiration and diffusion. If the treatment had substantially increased soil CO₂, this would likely have been reflected in the NEE measurements, and we would not have observed the increase in C sequestration. It is therefore possible that there was some misinterpretation of our results, and we are grateful for the opportunity to clarify this point.

Comment#52: In the Introduction section of the manuscript the elaboration on core scientific questions remains insufficient. While the experimental methodology underpins part of the work’s innovative merit, it is imperative to supplement a dedicated paragraph that explicitly clarifies the scientific rationale for investigating EW-induced effects on soil carbon from the perspective of carbon fluxes. Specifically, this part should elaborate on the fundamental distinctions between this flux-based perspective and direct soil carbon evaluation, as well as the significance of expanding to a flux-centric framework when assessing EW’s role in soil carbon sequestration.

We agree with the reviewer that the rationale of the study was not clearly laid out. We will correct the introduction accordingly, by deepening the literature context, and providing a proper research gap (“These contrasting effects illustrate the difficulty of isolating a single mechanism and highlight the need for integrative approaches that jointly consider inorganic sinks, organic matter dynamics, and secondary mineral formation when evaluating the true CO₂ removal potential of enhanced weathering (Steinwidder et al., 2025). Together, these processes illustrate that reliable estimates of carbon dioxide removal (CDR) through enhanced weathering must account for both inorganic and organic C pools, as well as the role of secondary mineral phases, rather than focusing solely on weathering rates.”). We hope it addresses the reviewer’s comment. This reply is also connected to the improvements in the introduction section from comment#10.

Comment#53: It is recommended to incorporate an experimental design figure into the supplementary materials to facilitate readers’ comprehensive understanding the crop ecosystem within a macro-scale and the carbon flux monitoring system.

We will add an experimental figure design into the “macrocosm details” box.

Comment#54: Line 244 The manuscript mentions a “different bootstrapping approach” for gappy DIC/Ca/Mg data, but does not detail how it differs from the standard bootstrapping used for soil C flux.

Thank you for pointing this out. We clarify how this bootstrap procedure differs from the initial one in the following sentence (“We generated empirical distributions of the concentration of the element (iC, Ca or Mg) in soil solution at the unit level (in order to keep the structure induced by depth and date). We then ran a generalized linear model with treatment, depth and their interaction as fixed variables and unit and date as random variables, and computed the average estimate and p-value of the effect of treatment across all iterations (n = 1,000).”), but we are happy to further emphasize this distinction if you feel it would improve clarity.

Comment#55: Result 3.1 Climate condition should be moved to Section 2.3 Climate simulations of the Material and Methods .

We will correct accordingly (see also comment #32).

Comment#56: The results section incorporates the discussion content, such as most of the content in 3.3. The results section should only present the results and move the explanations of the results into the Discussion section.

We will correct accordingly. Note that we will also add a new section in the material and methods to better introduce the Mg and Ca measurements.

Comment#57: Silicate weathering releases Ca²⁺ and Mg²⁺ (prerequisites for carbonate formation), yet no treatment differences in these cations were detected. The manuscript should clarify whether cation concentrations were measured in leachates (not just pore water) and discuss if plant uptake or adsorption to soil colloids explains the absence of leaching-key to ruling out carbonate formation

We understand that the reviewer means by “leaching” the Ca and Mg that would have left the macrocosm from the lower boundary of the lysimeter. Indeed our measurements were done on pore water only, not on leaching; we now clarify it in the manuscript. Indeed, we agree that the mechanisms suggested by the reviewer may be responsible for the absence of these elements in the soil solution; we will add these elements to the discussion.

Comment#58: Line 30 Enhanced weathering (EW)” and Line 345 “enhanced rock weathering (ERW)” are used interchangeably. Standardize to one term to avoid confusion.

We will correct accordingly. We will use EW throughout the manuscript.

Comment#59: The width of the table should be the same as the width of the page window.

We will correct accordingly.

Comment#60: Notable formatting inconsistencies are present across both the main text and supplementary materials of the manuscript. A comprehensive review and adjustment of the text, figures, and supplementary content are therefore recommended to ensure adherence to academic formatting standards.

We assume that this comment is an introduction to the following ones. If not, we would appreciate it if the reviewer could clarify their comment, as we were unable to identify any formatting inconsistencies apart from what is listed below.

Comment#61: Line 450 Extraneous spacing precedes the reference list

We assume the reviewer refers here to the page jump. We will remove it.

Comment#62: Table S1 lacks the horizontal lines at the top and bottom.

We will correct accordingly

Comment#63: The image resolution is insufficient for clear interpretation of details.

We assume the reviewer refers to Figure S1. It is unfortunately very difficult to embed such a complex figure on a word file with a proper resolution. However we generated the file as a pdf and will provide it to the editorial team if the paper is accepted for publication.

Comment#64: The y-axis font sizes in Figures S4 and S7 are excessively small, impeding readability.

We will correct accordingly

Comment#65: The line spacing in the legend of Figure S5 within the manuscript is notably irregular and fails to align with the consistent design style adopted for other figure legends throughout the work.

We will correct accordingly

Comment#66: The Discussion section of the manuscript inadequately integrates the isotopic research findings when elaborating on the impacts of EW on carbon flux and soil carbon.

We will correct accordingly (we suggest to add the following sentence in the discussion:” Isotope evidence also showed that the EW treatment did not directly interact with the atmospheric C pool instead of the CO2 coming from soil respiration.  ”).