the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 27 Feb 2026
Technical note: Verification of coastal enhanced weathering by tracking the dissolution of alkaline minerals: Theory and laboratory tests with olivine
Abstract. Coastal Enhanced Weathering (CEW) is a marine Carbon Dioxide Removal (CDR) method that adds ground alkaline minerals to shallow regions of the ocean in order to increase seawater alkalinity, i.e., its capacity for storing atmospheric CO2 as bicarbonate. While CEW is promising with regard to cost and scalability, it is an uncontained, “open-system” style of CDR, and presents significant challenges to effective measurement, reporting, and verification (MRV) of the process. In particular, quantifying how much alkalinity is released from an added amount of mineral is challenging as the minerals dissolve and release alkalinity over wide spatial and long temporal scales. Such quantification is further complicated by the fact that dissolved alkalinity is rapidly diluted below detectable concentrations. Here, we propose an approach to measure alkalinity formation that relies on solid sediment tracers to track mineral grains underwater and quantify how much they have dissolved over time. The amount of dissolution at any given point in time is proportional to the amount of alkalinity released. Thus, the approach aims to overcome the near impossible detection of alkalinity accumulation in the dissolved phase by tracking the loss of alkaline material in the solid phase. We describe a test of the fundamental aspects of this method including the measurement of the mineral and tracer content of a sediment sample, and the extent to which those measurements correlate with changes in seawater chemistry. We found that olivine dissolution significantly increased alkalinity in seawater, compared to control incubators. X-Ray Diffraction (XRD) was able to quantify the change in the olivine in the sediment (albeit with large relative errors) and automated particle counting methods were able to enumerate tracer particles when illuminated under UV-A light. These results serve as a proof-of-principle (and starting point) to further explore a promising way to measure alkalinity addition to the ocean resulting from CEW deployments.
Status: final response (author comments only)
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RC1: 'Comment on egusphere-2026-929', Anonymous Referee #1, 27 Mar 2026
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AC1: 'Reply on RC1', Alexander Milde, 17 May 2026
RC1:
General comment:
The technical note by Milde and Bach investigates the challenges of MRV in the OAE context. They approached this topic by exploring a mineral tracer, that should be able to help quantifying the amount of olivine dissolution and related alkalinity generation. This is an interesting and straight-forward approach, that could advance the field of MRV. In their study, the authors conducted batch experiments to investigate the usefulness of the tracer, i.e. Silicon Carbide.
While an alkalinity increase was clearly detected in their experiments, the tracer evaluation failed due to an increase in tracer counts after sediment incubation, meaning a decrease in tracer particle size. This was unexpected as no change in number or size of the tracer particles should have occurred and the authors attributed the changes to reactions during tracer shipping and storage and related high temperatures. As these challenges can always occur, I was surprised to only detect the ‘failure’ of the experiments when reading the main text and that it was not mentioned in the abstract. My first reaction was to recommend rejection of this manuscript as the experiments couldn’t evaluate the effectiveness of the tracer method and the other approaches to define alkalinity generation and CO2-sequestration by the authors (e.g. via XRD) contained large uncertainties. Nevertheless, in times as urgent climate change mitigation actions are required, I came to the conclusion, that this manuscript should be published anyway, as it will advance the research field in the sense that the experienced challenges can hopefully be avoided in future studies and mistakes avoided. Also failed experiments should be published in order to advance science on a timely manner. Therefore, I recommend publication of this manuscript after moderate revisions (see below) and only if the authors incorporate the fact, the results and reasons of the failed experiment in the abstract.
AC: The authors would like to thank reviewer #1 for their thoughtful comment. We have taken the comments about the clarity of the abstract to heart and will revise the abstract to highlight the places the experiment failed alongside the places that it yielded promising results. The specific type of tracer used here did not behave as expected, but we did see useful and ultimately promising results in the ability to enumerate the tracer particles that support the approach. On the whole, these results indicate that the method in question warrants a lot more work to scrutinize it, but what is presented here is a first important milestone that will help the research community with further exploration. In the spirit of transparent research and development (which is essential for marine CO2 removal) we feel that getting the wider research field to weigh in on and help shape the method going forward is the best course of action, especially given the urgency of addressing climate change. Despite the imperfect nature of these results, they are important to include as they illustrate and complement the theoretical description of the method. We believe that by grounding that theoretical description of the method in experiment we will facilitate a much better and more robust discussion and development of this potential, but highly needed, MRV technique. We appreciate that the reviewer shares our sentiment that this idea and results should be published to advance the field.
Specific comments:
Lines 147-148: Something is wrong in this sentence, I don’t understand: ‘…, side to err to as….’?
AC: This wording will be clarified. The point attempting to be made is that in real world situations there are always sources of error introduced to measurements, and in this case, the error introduced is always to the side of the measured value being less than the true value of mineral dissolved. While this is still error in the measurement, it is the preferable type of error as far as carbon crediting is concerned because it takes credit for less carbon being ultimately removed than was actually removed. This is as opposed to measuring an artificially high amount of dissolution, which would lead to over-crediting in a commercial scenario which would be a problem.
Line 149: I understand that this is just a first theoretical approach, but how well does one know the dispersal area after 1 year (or several) of mineral deployment? I assume this could create quite large uncertainties in the assessment as the identification of the regional distribution could be quite challenging at different scales and settings? I would recommend to do some sensitivity analyses to identify the impact on MRV based on these uncertainties.
AC: This is a valid point, and is a definite engineering challenge to work through in eventual deployment. However, the fact that the fluorescent tracers have a very low limit of detection in sediment samples means that we do not have to know the dispersal area before measurements are taken. We can sample in a grid pattern starting at the deployment location and expand the sampling area until we are no longer finding tracer particles in the samples. This eliminates the need to fully predict the sediment transport a priori, and in the authors opinion this is one of the major benefits of this potential method.
Line 184: Why is there serpentinite in the treatment group and not olivine? Or do you mean the ultramafic rock addition with serpentinite? Please clarify.
AC: We will clarify in the revised manuscript.
Line 206ff: If understood correctly, there was no shaking of the bottles. I wonder if particle movement, as it is common in coastal settings, would lead to particle abrasion and also abrasion of the tracer. By this, adding another level of uncertainty to the potentially inert character of the tracer. Have you tested the robustness of the tracer with respect to grain collision?
AC: This is a valid point, and will be an integral part of testing the robustness of tracers going forward. As noted in the manuscript, a new tracer construction method is needed, and development work on this is ongoing.
Line 218-219: I would add a comment or reference here, that you also conducted XRD analyzes as I was missing this information when reading this paragraph.
AC: Thank you, we will do this in the revised manuscript.
Line 551: Could you give examples of these areas? I find it challenging to come up with places, where mineral particles would not be subject to resuspension.
AC: There are certainly limited areas where this would be the case, however deeper deployments in areas where the natural bottom sediment is composed of silt sized particles would be subject to less resuspension than higher energy environments. In the revised manuscript we will provide examples.
Figure 2: Please add again a description of what the control and S1-4 is composed of (either legend or caption). I was searching this, when wondering what the causes could be for the increases in TA, pH and aragonite saturation in the control treatment. Is this discussed anywhere? This needs to be incorporated in the main text as it might indicate that the tracer is not as unreactive as initially thought or that reactions in the sand are inducing these geochemical changes. Are you sure it’s really only composed of quartz? Please clarify these points in your revision.
AC: This is a valid point and we will be sure to clarify and add these details in the revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-929-AC1
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AC1: 'Reply on RC1', Alexander Milde, 17 May 2026
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RC2: 'Comment on egusphere-2026-929', Anonymous Referee #2, 17 Apr 2026
This paper proposes a new approach for measuring mineral dissolution in coastal enhanced weathering (CEW) applications, using UV fluorescent tracer particles. The study uses seawater incubations with the tracer and olivine+quartz (treatment) and quartz (control). The tracers did not prove useful in measuring dissolution rates, however, as methodological issues affected their stability (size fractionation) over the course of the experiment. The authors make two main conclusions: 1) the tracer method is a promising tool for measuring mineral dissolution (despite the fact they were not ultimately useful in this particular experiment); and 2) olivine dissolution and alkalinity generation occurred in the treatments (based on alkalinity measurements, and inferred loss of olivine mass). The paper is overall well-written and the experiments explained clearly. I admire the risk taken here to explore a new methodology, and respect that “methodology papers” are a lot of work! That said, the data fundamentally do not support the proposed method – nor do they indicate a clear failure / dead-end. The paper could be improved with new data, resolving the methodological issues, to better assess the methodology.
- Major issues:
- The main issue is that the key aim of the paper – that tracers can facilitate quantification of mineral dissolution – is not demonstrated. I understand that this is a proof of concept, and completely welcome the unexpected results, but the authors’ conclusions are fundamentally flawed. L430: “we conclude that using UV fluorescence as a traceable characteristic in tracer particles is effective and could be suitable for operational deployment of this dissolution quantification approach”. And “Preliminary indications are that this method could possess sufficient resolution to meaningfully measure mineral dissolution, and corresponding alkalinity addition, in deployment scenarios.” But they have not shown that this approach works to quantify dissolution at all; in fact, they don’t use it in their results. They make this claim in reference to the fact that they were able to see the particles via UV fluorescence, which is not surprising, and was presumably known a priori. This is a great idea, and I appreciate the well-designed experiment. But the results as presented seem like an early experiment, prior to the necessary trial and error to get data of sufficient quality to test the hypothesis. The data simply do not answer the posed question.
- In addition to their key aim, they also use mineral mass measurements to estimate olivine dissolution at the end of the experiment. While this would have been complementary to the tracer-based dataset, it is not particularly novel or useful on its own. Also, they do not provide absolute masses –only relative percentages – so it’s not clear to me that there was not absolute loss, or loss across the different minerals from experimental artifacts. They acknowledge this potential later in the discussion (L506)
- Fundamental questions about the proposed method that are not adequately discussed:
- The paper broadly equates mineral dissolution with alkalinity addition. E.g., L73, “This loss of alkaline mineral would be used to infer the amount of alkalinity added to the seawater.” There are many ways alkalinity may be lost in sediments on short time scales following dissolution, with the consequence of no alkalinity added to the water column. (See Geerts et al review for discussion). The authors discuss this later, and suggest using a site- and mineral-specific alkalinity release factor. However, that factor is unknown given challenging MRV -- which the paper’s method is supposed to help with. (Plus, given different diagenetic environments, you might need an alkalinity release factor for every microenvironment your feedstock is dispersed to.) So there’s some circular logic here, and the issue at hand remains – we wouldn’t know the site specific alkalinity release factors required to use this method in the field.
- Sediment diagenesis and geomorphology considerations: “A perfect tracer will decrease in diameter at the same rate as the dissolving mineral particles do in order to maintain matching hydrodynamic properties, and therefore transport characteristics, to the mineral particles over the full dissolution period.” The decrease in diameter will depend on the mineralogical properties of the material and diagenetic environment. Given different mineralogies, I would think it's virtually impossible that the tracer will shrink at the same rate as the feedstock. It isn’t explained until the caption of Figure 1 that “the scenario of this experiment where an imperfect non-shrinking tracer was used.”.
- Minor issues:
- I’m curious why such small amounts of sediment were used (7.5 g = 0.1 to 3 mm depth)? Maybe explain.
- Figure 1 caption is far too long; the information should be part of the main text.
- Throughout the manuscript, I suggest caution with the assumption that dissolution equals alkalinity release, and adding words like “initial” or “preliminary” to indicate there may be subsequent losses. Instead of saying, e.g., “alkalinity formation”, it’d be better to caveat with “initial alkalinity release”.
- L41: I’m not aware of any CEW projects or research suggesting brucite for CEW (rather, for water column dissolution; brucite on sediments likely has ecology concerns). Similarly L89: lime is not appropriate for benthic CEW.
- L60: perhaps centuries, realistically?
- L63: sources?
- L421: the reason for choosing a high temperature should be explained in the methods.
- L423: Why would you expect this high level of dissolution? Citation?
Citation: https://doi.org/10.5194/egusphere-2026-929-RC2 -
AC2: 'Reply on RC2', Alexander Milde, 17 May 2026
RC2:
This paper proposes a new approach for measuring mineral dissolution in coastal enhanced weathering (CEW) applications, using UV fluorescent tracer particles. The study uses seawater incubations with the tracer and olivine+quartz (treatment) and quartz (control). The tracers did not prove useful in measuring dissolution rates, however, as methodological issues affected their stability (size fractionation) over the course of the experiment. The authors make two main conclusions: 1) the tracer method is a promising tool for measuring mineral dissolution (despite the fact they were not ultimately useful in this particular experiment); and 2) olivine dissolution and alkalinity generation occurred in the treatments (based on alkalinity measurements, and inferred loss of olivine mass). The paper is overall well-written and the experiments explained clearly. I admire the risk taken here to explore a new methodology, and respect that “methodology papers” are a lot of work! That said, the data fundamentally do not support the proposed method – nor do they indicate a clear failure / dead-end. The paper could be improved with new data, resolving the methodological issues, to better assess the methodology.
AC: The authors would like to thank Reviewer #2 for their thorough and thoughtful response. Broadly, we agree with the reviewer’s sentiment that the data does not fully support the method or indicate a clear failure or dead end! The goal of this early experiment and paper is to get the discussion of this method, which is a significantly different direction than the field is currently heading, started in the broader community as soon as possible. We hope by that laying out the theory of the method alongside the initial tests we will lay the foundation for a more robust discussion and exploration of this method than by either waiting to publish or attempting to publish the theoretical description of the dissolution quantification method on its own. As reviewer #1 succinctly put it, we hope that these imperfect results will “advance the research field in the sense that the experienced challenges can hopefully be avoided in future studies and mistakes avoided”. We have responded to the detailed comments below.
Major issues:
- The main issue is that the key aim of the paper – that tracers can facilitate quantification of mineral dissolution – is not demonstrated. I understand that this is a proof of concept, and completely welcome the unexpected results, but the authors’ conclusions are fundamentally flawed. L430: “we conclude that using UV fluorescence as a traceable characteristic in tracer particles is effective and could be suitable for operational deployment of this dissolution quantification approach”. And “Preliminary indications are that this method could possess sufficient resolution to meaningfully measure mineral dissolution, and corresponding alkalinity addition, in deployment scenarios.” But they have not shown that this approach works to quantify dissolution at all; in fact, they don’t use it in their results. They make this claim in reference to the fact that they were able to see the particles via UV fluorescence, which is not surprising, and was presumably known a priori. This is a great idea, and I appreciate the well-designed experiment. But the results as presented seem like an early experiment, prior to the necessary trial and error to get data of sufficient quality to test the hypothesis. The data simply do not answer the posed question.
AC: We agree with the reviewer that the data do not fully answer the question of whether this method will ultimately work or not and more work is needed to fully test the hypothesis. However, these early results do seem to indicate that the work to do the methodological improvements necessary is work worth doing. Part of the goal of this paper is, given the urgent nature of climate change mitigation, is to get the idea out there as soon as possible for as many people as possible to build on. While the data and results are not perfect, they are still useful and illustrate the proposed method better than a purely theoretical presentation would which gives everyone a better starting point from which to develop and evaluate this method. We believe a very transparent research process is the best course of action in this field, a sentiment shared and highlighted in both the Aspen Institute’s “A Code of Conduct for Marine Carbon Dioxide Removal Research” and in the “Guide to Best Practices in Ocean Alkalinity Enhancement Research”. In fact, the first “Key Message” in the introduction to the Best Practices Guide explicitly emphasizes this point, stating: “We recommend transparent sharing of all results of all experiments, irrespective of whether experimental outcomes are considered “positive” (e.g. affirmative of the experimenters’ prior assumptions), “negative”, or “neutral”. This includes full transparency of OAE research that provides additional complications for and/or roadblocks to OAE implementation (Oschlies et al).".
- In addition to their key aim, they also use mineral mass measurements to estimate olivine dissolution at the end of the experiment. While this would have been complementary to the tracer-based dataset, it is not particularly novel or useful on its own. Also, they do not provide absolute masses –only relative percentages – so it’s not clear to me that there was not absolute loss, or loss across the different minerals from experimental artifacts. They acknowledge this potential later in the discussion (L506)
AC: In a real-world scenario, where the sediment is not contained, the mineral mass measurements are required alongside the tracer enumeration to quantify dissolution as the tracer controls for dispersal related concentration changes, and so the authors push back on the assertion that these mass measurements are not useful. To the relative percentage point, even though we only report percentages in the current version of the manuscript, those percentages are directly related to absolute mass, and mass loss, given that we held the sample mass consistent over each measurement. There are potential experimental artifacts that we discuss, however the authors feel that that these mass measurements are still an important aspect to this work. We will improve the presentation and discussion of this in the revised manuscript.
Fundamental questions about the proposed method that are not adequately discussed:
- The paper broadly equates mineral dissolution with alkalinity addition. E.g., L73, “This loss of alkaline mineral would be used to infer the amount of alkalinity added to the seawater.” There are many ways alkalinity may be lost in sediments on short time scales following dissolution, with the consequence of no alkalinity added to the water column. (See Geerts et al review for discussion). The authors discuss this later, and suggest using a site- and mineral-specific alkalinity release factor. However, that factor is unknown given challenging MRV -- which the paper’s method is supposed to help with. (Plus, given different diagenetic environments, you might need an alkalinity release factor for every microenvironment your feedstock is dispersed to.) So there’s some circular logic here, and the issue at hand remains – we wouldn’t know the site specific alkalinity release factors required to use this method in the field.
AC: This a valid point and it is well taken by the authors. There are multiple mechanisms through which alkalinity can be lost in the pore water after initial addition but before making it to the overlying water column. In order to know the amount of alkalinity added to the water column, the value we are ultimately interested in, you need to accurately constrain and measure two values. One - the amount of alkalinity initially released into the aqueous phase, and two – the amount of that initial alkalinity release that escapes losses due to secondary precipitation and makes it into the overlying water column. The dissolution quantification method considered in this paper aims to accurately measure and constrain the first value, the initial alkalinity release. Yes, there still is difficulty and uncertainty in quantifying site specific release factors, but as we discuss in the manuscript, we believe this is a tractable problem with either experimentally derived or model derived release factors. With regards to the point that you would need many release factors for the many different microenvironments. This is true to get a theoretically perfect picture of the alkalinity release. However, we see this problem as similar to the problem faced by all field work of how many samples to take. More is better, but sampling faces real world constraints, and so you have to trade perfect measurement of the system via infinite samples with what is good enough to yield acceptable error bars. In this case, infinite release factors would be ideal, but we believe that a limited number of factors related to the actual variation in the deployment site could be sufficient for better constraining real-world implementation of this method. At the end of the day, the authors believe this technique can meaningfully increase our confidence in the amount of alkalinity released by accurately measuring mineral dissolution despite the method not fully eliminating the release generation factor difficulties highlighted here.
- Sediment diagenesis and geomorphology considerations: “A perfect tracer will decrease in diameter at the same rate as the dissolving mineral particles do in order to maintain matching hydrodynamic properties, and therefore transport characteristics, to the mineral particles over the full dissolution period.” The decrease in diameter will depend on the mineralogical properties of the material and diagenetic environment. Given different mineralogies, I would think it's virtually impossible that the tracer will shrink at the same rate as the feedstock. It isn’t explained until the caption of Figure 1 that “the scenario of this experiment where an imperfect non-shrinking tracer was used.”.
AC: The point to highlight is the fact that this experiment used an imperfect tracer is well taken and we will emphasize this in the revision. The comment also gets at the technical crux of this method – that it is very hard to create a tracer that decreases in diameter identically to the mineral of interest. This is a core aspect of the ongoing development of this method. In work done recently we have been able to create a prototype tracer by infusing the mineral itself with fluorescent dye through high pressure microcracking and subsequent dye infusion, thereby creating a tracer particle out of the mineral itself. Work is ongoing to thoroughly investigate the quality of the hydrodynamic match to the feedstock, however, given that they are the same material it seems highly likely that a very close match in diameters and hydrodynamic properties will be maintained over the entire dissolution range of interest. Due to the fact that we have created this promising path to a near ideal tracer we believe that this is not as fundamental an issue to the method as the reviewer supposes.
Minor issues:
I’m curious why such small amounts of sediment were used (7.5 g = 0.1 to 3 mm depth)? Maybe explain.
AC: This was to keep the expected alkalinity additions to the seawater below levels that would be expected to induce calcium carbonate throughout the experiment. We will add an explanation of this in the revised manuscript.
Figure 1 caption is far too long; the information should be part of the main text.
AC: We will include this change in the revised manuscript.
Throughout the manuscript, I suggest caution with the assumption that dissolution equals alkalinity release, and adding words like “initial” or “preliminary” to indicate there may be subsequent losses. Instead of saying, e.g., “alkalinity formation”, it’d be better to caveat with “initial alkalinity release”.
AC: This is a good point, one the authors fully agree with, and will make this distinction clear in the revised manuscript.
L41: I’m not aware of any CEW projects or research suggesting brucite for CEW (rather, for water column dissolution; brucite on sediments likely has ecology concerns). Similarly L89: lime is not appropriate for benthic CEW.
AC: This is noted, and the authors will provide more detail to support the use of these minerals or remove the reference to them.
L60: perhaps centuries, realistically?
AC: For some grind size and water temperature combinations centuries is certainly a possibility, but the authors are not aware of any proposed commercial deployments that are targeting centuries long dissolution timescales which is why it was not mentioned here.
L63: sources?
AC: This is a valid request and sources will be included in the revised manuscript.
L421: the reason for choosing a high temperature should be explained in the methods.
AC: This is a fair point and an explanation of this will be included in the methods.
L423: Why would you expect this high level of dissolution? Citation?
AC: This was based upon a shrinking core model of dissolution, using rates from Rimstidt et al. We will include an explanation of the calculation in the revised manuscript and provide sources.
Citation: https://doi.org/10.5194/egusphere-2026-929-AC2
- Major issues:
Data sets
Data for "Technical note: Verification of coastal enhanced weathering by tracking the dissolution of alkaline minerals: Theory and laboratory tests with olivine." Alexander Milde and Lennart Bach https://zenodo.org/records/18665602
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- 1
General comment:
The technical note by Milde and Bach investigates the challenges of MRV in the OAE context. They approached this topic by exploring a mineral tracer, that should be able to help quantifying the amount of olivine dissolution and related alkalinity generation. This is an interesting and straight-forward approach, that could advance the field of MRV. In their study, the authors conducted batch experiments to investigate the usefulness of the tracer, i.e. Silicon Carbide.
While an alkalinity increase was clearly detected in their experiments, the tracer evaluation failed due to an increase in tracer counts after sediment incubation, meaning a decrease in tracer particle size. This was unexpected as no change in number or size of the tracer particles should have occurred and the authors attributed the changes to reactions during tracer shipping and storage and related high temperatures. As these challenges can always occur, I was surprised to only detect the ‘failure’ of the experiments when reading the main text and that it was not mentioned in the abstract. My first reaction was to recommend rejection of this manuscript as the experiments couldn’t evaluate the effectiveness of the tracer method and the other approaches to define alkalinity generation and CO2-sequestration by the authors (e.g. via XRD) contained large uncertainties. Nevertheless, in times as urgent climate change mitigation actions are required, I came to the conclusion, that this manuscript should be published anyway, as it will advance the research field in the sense that the experienced challenges can hopefully be avoided in future studies and mistakes avoided. Also failed experiments should be published in order to advance science on a timely manner. Therefore, I recommend publication of this manuscript after moderate revisions (see below) and only if the authors incorporate the fact, the results and reasons of the failed experiment in the abstract.
Specific comments:
Lines 147-148: Something is wrong in this sentence, I don’t understand: ‘…, side to err to as….’?
Line 149ff: I understand that this is just a first theoretical approach, but how well does one know the dispersal area after 1 year (or several) of mineral deployment? I assume this could create quite large uncertainties in the assessment as the identification of the regional distribution could be quite challenging at different scales and settings? I would recommend to do some sensitivity analyses to identify the impact on MRV based on these uncertainties.
Line 184: Why is there serpentinite in the treatment group and not olivine? Or do you mean the ultramafic rock addition with serpentinite? Please clarify.
Line 206ff: If understood correctly, there was no shaking of the bottles. I wonder if particle movement, as it is common in coastal settings, would lead to particle abrasion and also abrasion of the tracer. By this, adding another level of uncertainty to the potentially inert character of the tracer. Have you tested the robustness of the tracer with respect to grain collision?
Line 218-219: I would add a comment or reference here, that you also conducted XRD analyzes as I was missing this information when reading this paragraph.
Line 551: Could you give examples of these areas? I find it challenging to come up with places, where mineral particles would not be subject to resuspension.
Figure 2: Please add again a description of what the control and S1-4 is composed of (either legend or caption). I was searching this, when wondering what the causes could be for the increases in TA, pH and aragonite saturation in the control treatment. Is this discussed anywhere? This needs to be incorporated in the main text as it might indicate that the tracer is not as unreactive as initially thought or that reactions in the sand are inducing these geochemical changes. Are you sure it’s really only composed of quartz? Please clarify these points in your revision.