The manuscript examines the effectiveness of slowly dissolving alkaline minerals at reducing atmospheric CO2 concentration in a global deployment scenario. A shrinking core model is used to calculate the depth profile over which alkalinity is deposited and this alkalinity flux is then coupled to an earth system model to examine the dynamics with which the alkalinity reaches the surface and causes an additional CO2 flux (relative to the counterfactual scenario). In itself, the paper sets out to explore a very straightforward question and uses reasonable approaches to arrive at an answer. The conclusion is that very finely ground olivine rock would be necessary for this approach to work efficiently.

However, what i feel is missing is a more comprehensive discussion about the realism of both the examined scenarios (open ocean, world wide, deposition of <2um olivine dust), the consequences of the conclusion that only very finely Olivine would work and the wider context of OAE development today, which is entirely focused on coastal deployment. 

I am not aware of any commercial or other large scale effort to spread finely ground olivine in open sea, precisely because of the issues raised in this paper (which have been known for some time) and other issues (such a turbidity, see below). However, coastal deployments of Olivine and Brucite are being actively developed and they do not suffer from the issues raised in this paper - this distinction should be made very clear in the conclusions and in a sentence in the abstract, because the manuscript focuses on a variant of OAE which is not actually being actively pursued by the industry and that context should be made clear.

I recommend expanding the discussion of these issues in the last few sections of the paper. The reader should not be left with the impression that Olivine cannot be feasibly used for OAE in general (it can, but only in shallow ocean deployments) or that open ocean OAE isn’t feasible (there are faster-dissolving alternatives to olivine, such as Ca(OH)2 and Mg(OH)2). These scope limitations are only briefly mentioned in Section 4.3 but I think they deserve much more visibility.

Specific comments:

L28 Some other studies also examined large scale (GtCO2) scenarios based only on coastal releases such as Feng et al. (2017) and He et al. (2023). It would be worth discussing these in contrast with the uniform alkalinity addition studies mentioned. 

L35 Also mention limitations due to turbidity and associated ecological problems.

L78 What happens when z0 exceeds the depth of the bathymetry at that point ? Is the alkalinity assumed to become buried or does it all immediately dissolve in the bottom cell ?

L95/ Eq (7)/ Fig 1b The exponential particle size distribution seems like an odd choice to me for several reasons. It doesn’t have any upper size cutoff - are we assuming occasionally giant chunks of olivine get through the grinding process ? My assumption was that during crushing processes there are sieves which only allow particles below a certain size to pass - is that not the case ? Either way, if particles larger than some size are effectively useless to OAE, any real-world process would presumably just sieve these out and feed them back to the grinder. This might be interesting to discuss somewhere ?

It seems from Fig A5 that the exponential PSDs are poor approximations compared to the power-law like relationship obtained from Renforth 2012. Why not use a powerlaw function instead ? Would be good to have a better justification for the theory developed in light of the experimental data presented.

Also because particle mass is a cube function of the radius distribution, the mean particle size maybe is not a good metric to describe the actual mass distribution, which is arguably more critical ? Therefore comparing uniform 1um particles to a exponential PSD with a mean particles size of 1um seems odd and perhaps leads, by definition almost, to the observed differences in dissolution properties.

I believe in the material processing world, quantities like P80 are used to describe grind sizes, which means a size at which 80% of the mass passes a sieve size, not 80% of the number of particles. Grinding costs are also usually expressed in terms of this, not in terms of mean particle size. I worry that using mean particle size unnecessarily distorts the picture.

L122-127 This section confused me a lot. You introduce an approximation on L123, assuming the particle doesn’t shrink while traversing the mixed layer, given the approximate equation on L123, followed by the exact equation 11. So far everything is good. 

L125 seems to justify using the approximation because Eq11  would require solving a third order polynomial. This doesn’t seem particularly hard - why is is this prohibitive ?

But then you proceed to say that Eq 10 leads to the same third order polynomial ?

So in the end, is Eq 10 an approximation which assumes no shrinking or is it exact ?

Does it imply tMLD from L122 is the same as that from Eq 11 (I assume not) ?

Do you have to solve the third order polynomial or not ?

I’d recommend rewriting this section. If what you end up is an approximation, just say that and justify its reasonable accuracy. If you end up with an exact result anyways, just derive the exact result from Eq 10 and or Eq 11.  If tMLD is just a stepping stone and all you care about is Chi and the Chi is exact, perhaps just derive that and  skip the discussion of tMLD calculations entirely ? Either way, try and clarify the explanation/justification here.

L164 landuse –> land use

L185 While true that reservoir feedbacks will cause the total CO2 removal from the atmosphere to be lower than the gross efficiency of 0.8-0.85, the same feedbacks also apply to emissions of CO2. But mCDR credits are generally measured as “negative emissions” (i.e. 1tCO2 of CDR offsets 1tCO2 of emissions and is credited as 1tCO2 “removed”). Previous work (https://iopscience.iop.org/article/10.1088/1748-9326/ad5a27 and https://egusphere.copernicus.org/preprints/2024/egusphere-2024-2150/) discuss this in more detail. 

I’d add a sentence explaining this relationship between gross and net efficiencies that the gross efficiencies are what applies to carbon credits.

One could potentially focus on expressing the efficiencies of the sinking rock-based simulations relative to the surface-dissolving reference simulation (though I understand there is already a lot of noise in these curves (Fig 3)).

Figure 3. These figures are difficult to parse. I’d recommend the following:

Panel a) Use dashed and dot-dashed lines to distinguish groups of related graphs. Perhaps Make the PSD graphs dashed and the surface dissolution dot-dashed ? 

Panel b) The annual average values are extremely noisy and impossible to parse. I dont see how they add any value plotted as such. I think showing the 31-year running means is sufficient to get your conclusions across. 

L260 This upwelling of deeper alkalinity is quite interesting. Is there a way to show a plot of vertical alkalinity evolution over time ? This would be cool to see for all the different runs shown in Fig 3. Figure A6 only shows pH difference. How about an analogous plot for ∆Alk ?

However that might wash out the effect mentioned in L260, perhaps doing a vertical cross-section of just the tropical upwelling regions ?

L301: …may further reduce the efficiency of olivine-based open-ocean OAE.

L361-363 This seems to confirm that mean particle size is not a good metric to describe the PSD of a a bunch of ground rock for purposes of OAE. P80 or mean mass size would be better. 

L363: Can’t simple sieving trivially remove the heavy tail of the distribution ?

L364-368 One major conclusion of the paper is tucked away in L364-368: Olivine is found to be unsuitable for open ocean deployment, because it must be ground <1um which is energetically and financially incompatible with affordable negative emissions. I would recommend expanding this section and discussing these economics more explicitly, stating estimated costs per tCO2 absorbed, for different grain sizes, accounting for efficiency losses: Coarse grinding is cheap but sinks too far, fine grinding dissolves but is too expensive. 

Section 4.3: Another issue with very finely ground rock is that it causes substantial turbidity which stresses many sea organisms. It would be worth discussing this here as it is another reason why super-finely ground olivine is likely a no go, even if grinding costs could be overcome. 

Can the authors add some analysis of the expected steady state turbidity increase (Total suspended solids) if OAE was deployed, say, at 100Mt/yr or 1Gt/yr scale, using the particle sizes used here and using a uniform deployment (as modelled here, ignoring shipping costs for the moment) over the whole ocean ? It seems the shrinking core and vertical distribution model could easily calculate the steady state for such a deployment.

How much would it change relative to typical ocean conditions and its variance ? Would it exceed federal EPA or EU limits for marine waters ?

How does the turbidity situation change with increasing dissolution rate (going to faster dissolving minerals) 

L375-L378: Shaw et al 2025 (https://www.frontiersin.org/journals/climate/articles/10.3389/fclim.2025.1616362/full) showed that precipitated Brucite (using alkalinity exchange) dissolves orders of magnitudes faster than mined brucite due to poorly formed crystals and would thus be very suitable for open ocean OAE. This would be worth mentioning here as a viable path forward for open ocean OAE. 

L368: Please add a paragraph in the conclusions emphasizing that this research does not preclude the deployment of coarser Olivine in shallow seas which is a viable option and does not suffer from the deep dissolution issues discussed in this paper. This is currently only stated briefly in one phrase on L368 and would likely be missed by readers who may come away with the impression that Olivine-based OAE is fundamentally infeasible. Shallow sea deployment of coarsely ground olivine appears to be economically feasible approach that is being scaled currently. FWIW it would be valuable to examine the CO2 uptake kinetics of shallow-ocean floor release of alkalinity in future work. 

Conclusions statement (section 5)

This section should be rewritten to give more concrete, stronger final conclusions of the clear implications and insights from the work done, in summarizing sentences. Many readers, especially in adjacent fields, will read the abstract and conclusions only so it’s worth reiterating every major insight in short form here. Some clear statements that should be included (non-exhaustive list):

1. Open ocean mCDR using olivine requires < 1uM particle sizes, which are noneconomical and potentially run into turbidity limits. 
2. For these reasons olivine addition is likely limited to shallow coastal regions (where it is currently being operationalized). Given conclusion 1., this mode of OAE should be a major direction of future research. 
3. Open ocean mCDR can still work with rapidly dissolving materials such as precipitated Mg(OH)2, NaOH or preequilibrated/predissolved approaches ( e.g https://www.science.org/doi/full/10.1126/sciadv.adr7250) which don't suffer from sinking problems or excessive, persistent turbidity. 

L415: The term theta (θ) appears but I can’t find a definition of it. Is this explained somewhere else?

This paper describes how particles, that might be used for ocean alkalinity enhancements (OAE) in order to reduce atmospheric CO2 are dissolving in the water column of the ocean and where they eventually might add alkalinity to the ocean as function of particle size and time. It is with respect to the dissolution process an update to Köhler et al. (2013) with some more details and the use of more recent parameters. The results show, that doubling the size of particles will increase the depth at which the particles are fully dissolved by a factor of 12, consequently reducing the alkalinity release near the ocean surface where it might influence the marine CO2 uptake capacity.

This is very nice piece of work and I have hardly anything to comment, which might improve the study, since it is already in a very good shape. 

My only comment is on the references to Yang & Timmermans 2024 and Yang et al 2025, (lines 311, 342) which commented on the results of Köhler et al (2013) and  suggested that due to instabilities in the water column - caused by the added material - particles might sink faster and therefore dissolve in deeper waters having a smaller effect on the CO2 update capacity of the OAE method. In these studies the authors assume an input of olivine of 15g/l citing laboratory studies where such numbers have been applied. However, in the open ocean context and the applied OAE used here and in other studies the amount of added particles is much lower. These 15g/l, or 15 kg/m^3 would transfer to 750 kg/m^2 if we assume a distribution over the whole of the ocean surface mixed layer with roughly a mean depth of 50 m.

In Köhler et al. (2013) at maximum 10 Pg of olivine was added to the ocean per year . Here, 0.14 Pmol alkalinity/yr is added in the control run (line 177), which is about 5 Pg of olivine/yr. Distributed across the ocean surface of the order of 360 10^12 m^2 (slightly smaller here when avoiding high latitudes) gives 28 g/m^2 or 0.028 kg/m^2. This is more than 4 orders of magnitudes smaller than the numbers used in Yang & Timmermans 2024. The authors here might therefore savely say, that the suggested instabilities which might increase the sinking speed of particles will probably only appear if particles are distributed in a very dense and localized setting.