The study by Bednarsek et al utilizes available data from the ocean acidification literature to evaluate how marine calcifiers could respond to ocean alkalinity enhancement (OAE). The analysis takes a statistical approach. The key concern is their use of the TA:DIC metric, which is considered indicative for carbonate chemistry changes induced by OAE due to its correlation with Omega (concerns detailed below). The value and conceptual basis of TA:DIC is currently unclear or possibly not valid. Therefore the authors would need to use another metric or provide a much better justification for the use of TA:DIC that is found on more than a correlation with Omega. I also have several other comments that warrant attention.

Major:

• The link between TA:DIC and OAE is perhaps not valid or at least not sufficiently well justified. In OA research, TA:DIC only changed because of increasing DIC. This, however, leads to other changes of relevant carbonate chemistry parameters (e.g. pH, CO2, HCO3-, CO32-) than a change in TA. There is no plausible explanation why the ratio of TA:DIC is a valid metric for OAE. The one argument made (control of TA:DIC on Omega) is not convincing so far  because Omega itself may not be such a relevant metric for biotic calcium carbonate precipitation (although of course the relevant metric for abiotic precipitation/dissolution). If the authors cannot show that TA:DIC is indicative for OAE then the analysis of biological responses relative to this ratio is also not sound. Thus, demonstrating the conceptual validity of TA:DIC (much beyond a correlation with Omega) is crucial.

For the derivation of TA:DIC, it also needs to  be considered with what state of OAE the concept correlates. Before equilibration with atmospheric CO2 or after?

One way forward could be correlation analyses of TA:DIC (where TA is left constant and DIC is varied, representative for OA), ideally using the data of the studies synthesised here. It could then be explored if TA:DIC is a useful metric for a specific transient state of OAE (e.g. unequilibrated or equilibrated with the atmosphere). However, if TA:DIC does not reflect carbonate chemistry changes of OAE more comprehensively (much beyond an Omega correlation) then the authors should use another metric to correlate their biological responses with.

Another question in this context is: If TA:DIC is used as a proxy for Omega, why wasn’t Omega used in the first place?

Finally, ratios such as TA:DIC do not consider absolute concentrations, which is another potential  weakness for a metric that has not been derived from physiological theory. This is particularly problematic because most of the data is sourced from ocean acidification research, which is looking at the other direction of the pH scale.

• The methods require a much more thorough description of what has been done. Some important steps are insufficiently clarified (see specific comments below).

• What was the rationale for using GLODAP data to derive correlations between TA:DIC and Omega? Wouldn’t it have been more reasonable to use data from the individual studies. Furthermore, how were temperature (salinity) differences between studies taken into account, which also affect Omega but not TA:DIC.

• The statistical approach is enigmatic to me. I am unsure if it is insufficiently described or I am lacking statistical knowledge (quite possibly the latter). Hopefully the other reviewer has better understanding and provide a robust review.

Other comments:

Line 24: So far OAE has no relevance for climate change mitigation.

Line 30: success or social license?

Line 40: No parabolic responses?

Line 41ff: What does realistic refer to here? That the conditions in most lab studies are not realistic wrt perturbation magnitude? Also, what  would be a realistic perturbation. (I agree with your point but think this is not thoroughly backed up at this stage).

Line 46f: It is totally unclear at this stage what the TA:DIC ratio is a proxy for and why it is helpful. This must either be explained or taken out of the abstract.

Line 48: Unclear what framework you are referring to. TA:DIC? Needs specification.

Line 69: CDRs is a weird plural. Removals?? Do you mean marine CDR methods?

Line 78: Some OAE methods are well beyond concept stage (see Eisaman et al., 2023)

Line 100: adaptation or acclimation? (I think you mean the latter).

Line 109: Alkaline or “higher pH”. Strictly speaking OA still investigated alkaline conditions wrt pH.

Line 121: Unclear how a systematic framework should help here. Vague term.

Line 139: The sentence implies that massive applications will happy anyway, in which case the environmental assessment before would implicitly have no influence on whether they are implemented.

Line 153: Based on what criterion were studies selected? Were all studies selected that were found by browsing? Or the first X hits?

Line 153: Were temperature differences between treatments in the OA studies considered?

Line 242: Unclear how NaOH was added to the TA:DIC ratio.                                               

Line 242: Unclear why a parabolic response is by default a negative response. This requires additional justification.

Figure 2 is unclear. Is this the entire dataset? Or a specific subset of data from various species. It is also unclear if each datapoint is a treatment level from an individual study.

Line 270: The “not strong” correlation between Omega and TA:DIC basically underscores that this metric is not representative of OAE.

Line 308: 98 or 96?

Line 373: How do you convert a response observed as TA:DIC ratio into a delta_concentration above which thresholds are reached?

Line 408: Several decades is exaggerated.

Line 412: while…while

Line 446: An interesting question would be if the results here are consistent with predictions for species where predictions are possible due to mechanistic understanding.

Line 466: The study by Albright did not show higher calcification rates but higher net calcification in a reef, which according to the authors could be due to reduced dissolution of the reef platform.

Line 553: Unclear how the framework would be able to establish baseline conditions, which vary in time and space. If a new framework is proposed here then it should be spelled out much more thoroughly. It is currently very vague.

Overall assessment: 

This is a timely and significant contribution and I applaud the authors. This manuscript is ambitious, covering a range of relevant species for calcification rate responses to OAE, and will be of interest to biological oceanographers, ecologists and the wider carbon removal community and industry. The paper has a fantastic coverage of species and I really like the focus on functional groups; this is a sensible way to think about ecosystem response to OAE, in terms of what function each of these organisms play in the marine food web and carbon cycle more generally e.g. biological and inorganic carbon pumps. I really enjoyed reading the paper and thought it was generally well written and scoped. However, I have some major points raised below and also some more minor under "other comments". The conclusions of the study are solid - there should be more realistic manipulations of TA for responses of biological organisms in academic studies, and this is a fair interpretation of the data. Statistical analysis seems fair. 



Major points for revision: 

1. Better elucidation of link between TA:DIC and Ωar needed. For example, in the text introducing the rationale, it is just described as TA:DIC being "essentially" related to Ωar, however this relationship is not explained in any depth and then in Figure 1, TA:DIC/Ωar is plotted on the x axis of the graphs, making an assumption that they are equivalent for those purposes. I think TA:DIC is a fair proxy for Ωar, but should not be plotted in a way that misleads to suggest they are functionally equivalent and could be 1:1 swapped out for one another in graphs such as those shown in Figure 1. A lot of this links back to methodology for this relationship being used which is shown in Figure 3; perhaps moving this graph to earlier in the flow of the manuscript could help to clear up some of this confusion. 
2. It seems questionable that GLODAP should have been used, the data logically to me should have come from the individual studies relevant and used in this study; I am unclear of the reasoning here and it does not seem well justified to be using global datasets for mapping some of these responses, but I note this justification is not well detailed in the text and could be a lack of explanation rather than a fundamental flaw in the design of the study.  
3. Not enough examination of what the actual impact of increased/decreased calcification rate would be in the manuscript. This is generally discussed in the context of biological responses to OAE, insinuating that any change is a bad change - this is not true - we have to think about this in the context of some organisms having decreased calcification under acidification scenarios, so some increase in calcification rate for these organisms could actually represent a bounce back to pre-acidification conditions. Overall, important to understand that any intentional manipulation of the earth system like OAE will have an impact, but the actual "negativity" of the impact needs to be a nuanced and detailed discussion, which I think this manuscript could benefit from significant additional discussion on this in the Discussion section of the manuscript. Places where this is particularly relevant: lines 562-564 and onwards.

Other comments: 

• Generally found the presentation of the different categories of response e.g. linear +, linear -, exponential +, exponential -, etc a bit confusing, particularly in Figure 6 and 7. I wonder if a box calling out exactly what fits into each of those categories and what they mean would be helpful for the reader to refer to. 
• line 483-485: not a sufficient explanation of the biological mechanisms involved in bicarbonate impact moderation in crustaceans 
• line 552: should read, such "a" guide
• line 559: should be "better informing further experimental work" 
• line 585: when "the" grazing effects included - "the" should be removed 
• line 589, from "a" not the "the" biogeochemical perspective 
• line 600-601: NaOH is not a carbonate-based compound
• line 605: "based" after OAE should be deleted
• line 609: should be "were" not "was" used
• line 618-619 - second part of clause not necessary, can be deleted
• One of the major conclusions of the study is that the study is aiming to be used by the community to identify species that are at the largest risk of a "negative" response, or have the greatest uncertainties in their potential responses. However, nowhere in the paper is there a succinct summary of what those species are, in a box, or in a section, or a table. I think something like this would greatly improve the impact and applicability of the paper for the intended audience to use it, and the manuscript would be improved by this
• line 626: replace "the" with "further" experimental work 
• line 630: add "an" experimental framework