Clark et al. describe coccolith culture experiments used to constrain how oxygen-18 fractionation between coccolith calcite and water, carbon-13 fractionation between coccolith calcite and DIC, and coccolith calcite D47 values vary as a function of environmental parameters and/or coccolithophore species. They observe 18O and 13C effects generally consistent with prior culture-derived observations although, in their words "no clear physiological conclusions can be drawn on the source of these vital effects". They also find that their coccolith D47 values are greater than expected from culture conditions based on a generally well-accepted calibration study of Anderson et al. (2021). Based on these results, they argue that a distinction should be made that "inorganic" and "biogenic" carbonates follow distinct calibration relationships, while "all previous biogenic calibrations can be used interchangeably".

The amount of hard work required to successfully run the culture experiments presented here should not be underestimated. As far as I can tell, this part of the work follows best practices, and the isotopic results reported here are beyond any doubt potentially useful and relevant to the issues discussed in the manuscript.

I am not a specialist of coccolith vital effects, particularly when it comes to carbon-13, but the discussion of oxygen-18 vital effects is far from perfect (see comments below). What's more, when it comes to the actual discussion of 13C and 18O vital effects manifested in these culture experiments, the reader gets the impression that not much new was learned from these particular experiments. Is this really the case? I suspect that a more careful discussion of this part of the results would improve the manuscript, making it useful to a wider audience beyond clumped isotope aficionados.

But the authors' main interest clearly lies with the clumped isotope story here. They rather bluntly (in my opinion) argue for a new distinction between biogenic and inorganic calibrations of D47, ignoring some important details along the way: for instance, that some of their "biogenic" calibrations combine biogenic and synthetic samples, as do De Winter at al. (2022); or that some biogenic data sets unmentioned in the discussion (Huyghe et al., 2022) offer compelling evidence of good agreement between biogenic and inorganic calcite.

For some reason, the elephant in the room — ie that the apparent offset between the coccolith D47 values presented here and those predicted using inorganic calibrations could very well reflect non-negligible isotopic disequilibrium/kinetic fractionation effects, which would not likely depend only on temperature — is not seriously taken into consideration.

With all due respect, arguing that "a constant biological mechanism is causing [an] offset of biogenic relative to inorganic carbonates" is so vague as to border on the meaningless. Biocalcification is still governed by physics and chemistry, it's not based on qualitatively different laws of nature. Furthermore, we have ample evidence that the following bio-related carbonates have D47 values indistinguishable from inorganic equilibrium values:

- lacustrine carbonates [0 to 4 degC] associated with microbial mats analyzed by Anderson et al. (2021)

- planktonic foraminifera [0 to 25 degC] analyzed by Peral et al. (2018) & Meinicke et al. (2020); see Daeron & Gray for further discussion

- calcitic bivalves [-2 to 27 degC] analyzed by Huyghe et al. (2022)

- aragonitic bivalves [1 to 3 degC] analyzed by De Winter et al. (2022)

One may instead argue that the coccoliths cultured here and the fast-growth bivalves cultured by De Winter et al. (2022) and Huyghe et al. (2022) are out of D47 equilibrium, while the rest of the inorganic, foraminifer, bivalve, and lacustrine samples from Anderson et al. (2021), Fiebig et al. (2021), Peral et al. (2018), Meinicke et al. (2020), and Huyghe et al. (2022) all appear to agree within analytical uncertainties.

As a result of the issues summarized above, this manuscript offers a disheartening contrast between what seems to be excellent, carefully-performed culture experiments, rather minimal/vague discussion of carbon-13 and oxygen-18 vital effects and very poorly supported claims about clumped isotope calibrations. Regrettably, I cannot recommand anything but rejection at this point. The data shown here may be of high quality, but the corresponding discussion should in my opinion be profoundly improved using much more solid arguments than is currently the case. Alternatively, if the authors persist in arguing for their current conclusions, they should drum up very strong evidence to support their strong claims. I am afraid this would amount to a new submission in both cases.

Collected comments

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- [Title] "clumped isotope equilibrium with seawater" is a rather surprising turn of phrase. Clumped isotope equilibrium is achieved between the different isotopologues of carbonate but not between the carbonate and water phases, contrary to oxygen-18 equilibrium.

- For some reason table 1 does not report either pCO2 or pH. Is that to be expected? These would seem like important parameters.

- in the abstract and elsewhere (see below), the phrase "do not have a significant effect" is a very ambiguous statement. Is it not significant because it is very small (e.g., <1 deg C equivalent) of because the observations are not very precise? When issuing these statements it is almost always worthwhile to state something like "no significant effect at the X ppm level". Needless to say, the implications are quite different depending on the value of X.

- The last sentence of the abstract ("Thus, all biogenic specific calibrations can be used interchangeably and must be used for the reconstruction of calcification temperatures in biogenic carbonates.") is an extremely strong statement, which is not supported by the currently available evidence, and with a high potential of being misused to justify arbitrary interpretations in the future.

- The sentence explaining clumped isotopes in lines [25-26] is poorly worded. Abundance of 13C-18O bonds primarily increases with d13C and d18O, with a second-order thermodynamic effect. Thus what increases as T decreases is the ratio between the actual 13C-18O abundance and the corresponding stochastic (predicted) abundance.

- Lines [30-34] seem to contradict the conclusions. For the conclusions of the manuscript to drastically upend prior ideas would require very strong new evidence and careful reassessment of preexisting evidence, which is simply missing.

- Line [42] Jautzy et al. is not biogenic

- It should be expected by by default, particularly in a EGU journal, that raw analytical data be provided to allow for future reprocessing efforts.

- The comparison of cleaning methods is always useful, as many of these efforts are never formally published.

- [173] To clarify: IAEA-C2 was treated as an unknwon sample? What is the long-term SD of its replicate-level D47 measurements (is this the sigma values quoted on line 174)? How many IAEA-C2 replicates were measured?

- Do analytical uncertainties account for standardization errors in any way?

- [190] How was the DIC uncertainty determined? Surely not by computing the SD of two repeatd measurements, I assume.

- [213] minor comment: using the SD of repeated d13C measurements (N=?) is reasonable when dealing with random noise, but if d13C values are found to be systematically drifting, it might be more accurate to characterize uncertainties using the total range of measured values.

- Is there any interpretation of / conclusion to the results of section 3.1.2 (Carbon isotopes)? If there are none, why include these results at all? It seems like a missed opportunity.

- [260] "The Δ18Oc-sw is thus genus- but not species-specific." That is a true statement for this data set. Whether it applies in general, or simply to other species of the same geni, or to different experimental conditions, would require a better physical understanding of the processes driving oxygen-isotope fractionation.

- [265-266] "There is no [clumped isotope] difference between species or genus at given temperatures." Again, this statement is very general but should be qualified (no obvious difference at the X ppm level).

- [269-271] "in order to fully evaluate potential vital effects in the Δ47-temperature relationship in coccolith calcite, we first characterize and discuss the vital effects in carbon and oxygen isotopes and compare them to previous culture studies." But this is never actually done (ie, discussing D47 equilibrium/disequilibrium in the context of oxygen-18 and carbon-13 disequilibrium).

- [280-281] "An increase in CO2(aq) relative to the cellular carbon demand will result in a decrease in Δ13Cc-DIC": This sentence simply repeats content from the previous one.

- The carbon-13 discussion raises seemingly interesting observations (that Δ13Cc-DIC does not appear to be negatively correlated with [CO2aq], contrary to model predictions). But after reading this section we don't really know if this is a problem with the models or if these models would actually predict a lack of Δ13Cc-DIC/[CO2aq] correlation for these particular experimental conditions.

- [294-295] "[equilibrium oxygen isotope fractionation between calcite and water is inferred to be represented by] laboratory experiments using 295 carbonic anhydrase (CA) to maintain oxygen isotopic exchange between DIC and H2O (Watkins et al., 2013; 2014)." This is simply wrong, as clearly stated by various authors over the years, including for example Watkins et al. (2013), who wrote that "based on this and the comparison to Ca isotopes, it is likely that neither ours nor any other experimental study has yielded the equilibrium value of Δ18Oc−w , which could be larger than the measured values by about 2‰."

- [296-297] "Non-equilibrium fractionation effects [manifest as] lower Δ18Oc-w". As written, this statement suggests that non-equilibrium fractionation is always associated with 18O depletion. This is clearly not the case for effects caused by CO2 degassing (Guo et al. 2020, GCA).

- [297-298] "This effect presumably occurs because calcite forms from both bicarbonate and carbonate ions in proportion to their abundance in solution" That might be in some cases, but not necessarily, see Devriendt (2017) model and discussion.

- [300-301]: "This process is illustrated by the ‘kinetic limit’ in Fig. 3" This kinetic limit is actually the "fast-growth" limit described by Watkins et al. (2014), where crystallization fluxes are an order of magnitude greater than the opposing dissolution fluxes. It exists at all pH values (but the value of the "fast-growth" Δ18Oc-w limit varies as a function of pH). The "kinetic limit" equation in the caption of fig. 3 is attributed to Watkins et al. (2014) but I could not find its origin in that paper. What's more, there is no mention that this "fast-growth" limit varies as a function of pH, nor of what pH was used to compute this formula. Finally, the text as written does not make it clear at all that these concepts only apply to DIC-cc fractionation, which are additively combined with disequilibrium fractionation between water and DIC.

- [307-310] "Models also suggest this for biogenic carbonates such as foraminifera and bivalves, as the magnitude of potential Δ47 disequilibrium is below the current analytical resolution for Δ47 measurements (Defliese and Lohmann, 2015; Watkins and Hunt, 2015; Devriendt et al., 2017)." There are several datasets providing evidence for biogenic calibrations being statistically indistinguishable from inorganic/equilibrium relationships (eg Anderson et al., 2021; Daeron & Gray, 2023). Also, Devriendt et al. (2017) do not consider clumped isotopes at all.

- [344-347] The emphasis on using a bivariate regression method does not seem warranted, given that errors in Y are about 100 times larger than errors in X.

- [349-355] Starting with a G. oceanica regression and then adding the other two species is not the traditional way of performing such "significance evaluations", and for good reason. A more acceptable approach is to perform some kind of ANCOVA analysis, as was done by Petersen et al. (2019) for example.

- [350-351] "each Δ47 measurement and uncertainty is taken individually as to have an equal contribution of each datapoint to the final calibration." Doing so artificially decreases the X error by a factor of sqrt(N), where N is the number of replicates for a given experiment, because the N data points (X,Y) are wrongly treated as having independent errors in X. Although this is ultimately irrelevant given that errors on Y very strongly dominate the regression weights (see above), it is wrong to present this as a sound approach.

- [354-355] "All regression lines fall within error of each other, which shows there is no species- or genus-specific vital effect on the Δ47-temperature relationship" As pointed out above about section 3.2, This statement might be true in the context this particular data set, with analytical uncertainties of a given magnitude, but for it to be useful in a more general context — particularly paleoclimate reconstructions —, you need to quantify this level of uncertainty. It would be very different to write "no vital effect on D47 larger than 0.001 ‰" and "no vital effect on D47 larger than 0.020 ‰". I do not need to belabor that point; in the first case, this means that using a coccolith-specific calibration is unlikely to ever have a detectable effect given current analytical limits. In the second case, this means that reconstructing coccolith paleotemperatures based on an equilibrium D47 calibration may or may not produce systematic bias on the order of 20 ppm (~7 degrees C). It is crucial to know where we currently stand on this spectrum.

- Section 4.5 appears superfluous. As pointed out in the text, the results of Katz et al. (2017) predate the Intercarb scale and can probably not reliably be converted to match the new data. So why attempt to combine data measured in different scales, then decide to use the previous regression anyway? Odds are that someone will eventually decide to disregard these methodological issues and use this combined equation anyway. Why facilitate bad practice?

- Section 4.5: The authors are apparently aware of the recent study by Daeron & Gray (2023), since they cite it and use one of their calibration equations, but Daeron & Gray argued, rather convincingly in my opinion, that the foram temperatures originally assigned done by Peral et al. (2018) and Meinicke et al. (2020) were biased by up to several degrees. It is thus awkward to cite Daeron & Gray and still go with the original, biased calibrations of Peral et al. & Meinicke et al. without taking the trouble to spell out why Daeron & Gray's claims (that the original temperature assignments should be corrected, and that planktonic foraminifera D47 agrees well with inorganic equilibrium calibrations) should be disregarded.

- [404-405] Regarding brachiopods, it is clearly problematic that their D47 does not only vary with temperature, as a result of DIC disequilibrium, as argued independently by Letulle et al. (2023) and Davies et al. (2023). Regarding the De Winter et al (2022) calibration, it should be pointed out that they analyzed (A) Arctica islandica with slow growth rates cultured at 1-3 degC and (B) Arctica islandica with growth rates >10 times greater than the previous ones, cultured at 15-18 degC. As reported by De Winter at al., Group A agrees quite well with Anderson et al., etc, but group B yields D47 values up to ~0.02 ‰ greater than expected from Anderson et al. It would be reasonable to wonder the results of group B reflect disequilibrium effects driven by very rapid growth rates, just like those observed by Huyghe et al. (2022) in juvenile oysters. But at any rate, the comparison shown here in fig. 8 does not use De Winter at al.'s Arctica islandica regression (their eq. 2). It is regrettably not stated which of De Winter's equations is used in fig. 9, but it should be noted that several of the calibration equations proposed by De Winter et al. include a very diverse mix of inorganic and biogenic samples up to 850 deg C. If one of these is used to argue for a distinction between "biogenic" and "inorganic" D47 calibrations, it would obviously be a major problem.

- [422-423] "It is important to note that the vital effects in the coccolith carbon and oxygen isotopes have no impact on their Δ47". Again (cf above), this statement must absolutely be quantified to be meaningful in any way.

- [423-425] Regarding the statement that theoretical models predict undetectable D47 disequilibirum even in the presence of detectable d13C and d18O disequilibria, this is simply not the case, as it is controlled by a free, unconstrained parameter ("epsilon" in Watkins & Hunt, 2015), which may or may not be equal to zero (cf fig. 6 of Watkins & Hunt).

The study by Clark et al. presents clumped isotope data based on cultured coccoliths and reports a coccolith-based ∆₄₇–T calibration. While the methodology is impeccable, the study lacks a rigorous interpretation of the results and contains ambiguous statements.

First, although the study is about “vital effects”, it is not clear what the authors mean by this broad term. Coccoliths grow their hard parts by completely different biomineralization mechanisms than corals, mollusks, or brachiopods. For these macro-organisms, “vital effects” can include, e.g., fractionation by CO₂ diffusion, CO₂ absorption, and crystal surface effects. Are the same effects also relevant for coccoliths? Are there other effects potentially leading to disequilibrium that are related to photosynthesis? It would be crucial to describe or, better, demonstrate with a figure what “vital effects” are expected specifically for coccoliths. One last thing to add here is that the authors often compare coccoliths with other biogenic carbonates while discussing vital effects, which assumes that all these organisms are impacted by the same “vital effects”, which is not necessarily the case. The fact that the apparent coccolith temperature-∆47 relationship is similar to other biogenic calibrations is likely just a coincidence, partly due to the fact that differences are not resolved.

Second, the authors conclude that coccoliths are not affected by disequilibrium effects, which is the opposite of what their data shows. I believe this comes from a misinterpretation of what isotope equilibrium is: there is only one clumped equilibrium for a given temperature, and everything that shows an offset is, by definition, not in equilibrium.  The authors write that coccoliths show an offset relative to inorganic carbonates. Inorganic carbonates, such as in the (Anderson et al., 2021), the (Daëron et al., 2019), and the (Fiebig et al., 2021) papers, are slow-growing and thus thought to reflect (near) thermodynamic equilibrium. If something shows an offset to these inorganic calibrations, it can be suspected that it is due to “vital effects”. Otherwise, reasoning is necessary as to why biogenic carbonates represent equilibrium, and slow-growing carbonates don’t. Additionally, the authors show prominent oxygen isotope disequilibrium effects. Irrespective of how the clumped data compares to other calibrations, what carbonate growth model makes it possible that oxygen isotopes are in disequilibrium while clumped isotopes are not?

In summary, the presented data is excellent and has the potential to make a significant contribution to the scientific community. However, in its current state, the paper resembles an imprecisely interpreted dataset that is surely not at the level of the journal. I hope that the authors will consider expanding their study so that their paper can be informative for a broader audience and have a higher scientific impact.

Line by line comments:

Title: for clumped isotope equilibrium it doesn’t matter what the ambient fluid is

L8: “all follow”: disagree, biogenic carbonates such as brachiopods and corals do show disequilibrium effects documented in many publications

L15: The literature is saturated with calibration studies. To catch the attention of the reader, the authors may want to make it clear in the abstract what is new in their study compared to previous studies, e.g.,  higher precision, more species analysed?

L21: Strongly disagree. No one would even consider using, for example, a foraminifera calibration for a mollusk.

L40: Consider adding (Thiagarajan et al., 2011), (Kimball et al., 2016), (Spooner et al., 2016), and (Davies et al., 2022) for corals, and (Bajnai et al., 2018) and (Davies et al., 2023) for brachiopods. Also, even if some biogenic carbonates fall within the confidence interval of a compilation-based (inorganic) calibration, they may still exhibit disequilibrium effects, that are e.g., not resolved.

L51: This statement is only true for mollusks if one wants to do a high-resolution study.

L60: What are coccolith vital effects?

L69: Do the two investigated genera have distinct calcification mechanisms that made the authors expect genus-specific effects?

L75: Did the authors observe any culture stress-related effects e.g., in morphology? Are there signs of carbonate dissolution?

L149: “reacted” may not be the correct word choice here

L185: To avoid the excessive use of abbreviations (e.g., CRM, CRLS, ETF, TLE …), the authors may consider the rule of thumb to only introduce an abbreviation that appears three or more times in the text.

L198: The correct notation is either δ²H or δD, but not δ²D

L203: Can you give a mean value here for the reproducibility?

L265: Consider adding “no ‘resolvable’ difference”

L349: Does this mean that your regression errors are likely underestimated?

L381: (!!) The authors wrote that the previous coccolith clumped studies were published before interlab standardization. What is the basis for a direct comparison of the values published in those studies and here? Did the authors recalculate the values by normalizing them to common standards?

L393: Why is it an “MIT” calibration?

L443: The study did not attempt to fit coccolith data into a calcification model, which is probably why no physiological conclusions could be drawn.

Figure 8: (#1) This figure is overcrowded and difficult to decipher. Suggest not displaying sample data from other studies but only the regression lines. (#2) Please consider plotting the calibration lines only within the temperature range they were made for.

Figure 3: The kinetic limit in the (Watkins et al., 2014) paper relates to the pH-dependent incorporation of the DIC species in the carbonate. However, the simple comparison presented here implies that this is the only “vital effect” that is relevant for coccoliths. However, it may as well be that some fractionation effects drive the O isotope composition of the carbonate in one direction, whereas others in the other direction, and they cancel out. The point is that this is not known without detailing the calcification model and the possibly occurring fractionation effects.

References cited in the review:

Anderson, N. T., Kelson, J. R., Kele, S., Daëron, M., Bonifacie, M., Horita, J., Mackey, T. J., John, C. M., Kluge, T., Petschnig, P., Jost, A. B., Huntington, K. W., Bernasconi, S. M., & Bergmann, K. D. (2021). A unified clumped isotope thermometer calibration (0.5–1100°C) using carbonate‐based standardization. Geophysical Research Letters, 48(7), e2020GL092069. https://doi.org/10.1029/2020gl092069

Bajnai, D., Fiebig, J., Tomašových, A., Milner Garcia, S., Rollion-Bard, C., Raddatz, J., Löffler, N., Primo-Ramos, C., & Brand, U. (2018). Assessing kinetic fractionation in brachiopod calcite using clumped isotopes. Scientific Reports, 8, 533. https://doi.org/10.1038/s41598-017-17353-7

Daëron, M., Drysdale, R. N., Peral, M., Huyghe, D., Blamart, D., Coplen, T. B., Lartaud, F., & Zanchetta, G. (2019). Most Earth-surface calcites precipitate out of isotopic equilibrium. Nature Communications, 10, 429. https://doi.org/10.1038/s41467-019-08336-5

Davies, A. J., Brand, U., Tagliavento, M., Bitner, M. A., Bajnai, D., Staudigel, P., Bernecker, M., & Fiebig, J. (2023). Isotopic disequilibrium in brachiopods disentangled with dual clumped isotope thermometry. Geochimica et Cosmochimica Acta, 359, 135–147. https://doi.org/10.1016/j.gca.2023.08.005

Davies, A. J., Guo, W., Bernecker, M., Tagliavento, M., Raddatz, J., Gischler, E., Flögel, S., & Fiebig, J. (2022). Dual clumped isotope thermometry of coral carbonate. Geochimica et Cosmochimica Acta, 338, 66–78. https://doi.org/10.1016/j.gca.2022.10.015

Fiebig, J., Daëron, M., Bernecker, M., Guo, W., Schneider, G., Boch, R., Bernasconi, S. M., Jautzy, J., & Dietzel, M. (2021). Calibration of the dual clumped isotope thermometer for carbonates. Geochimica et Cosmochimica Acta, 312, 235–256. https://doi.org/10.1016/j.gca.2021.07.012

Kimball, J., Eagle, R., & Dunbar, R. (2016). Carbonate “clumped” isotope signatures in aragonitic scleractinian and calcitic gorgonian deep-sea corals. Biogeosciences, 13(23), 6487–6505. https://doi.org/10.5194/bg-13-6487-2016

Spooner, P. T., Guo, W., Robinson, L. F., Thiagarajan, N., Hendry, K. R., Rosenheim, B. E., & Leng, M. J. (2016). Clumped isotope composition of cold-water corals: A role for vital effects? Geochimica et Cosmochimica Acta, 179, 123–141. https://doi.org/10.1016/j.gca.2016.01.023

Thiagarajan, N., Adkins, J., & Eiler, J. (2011). Carbonate clumped isotope thermometry of deep-sea corals and implications for vital effects. Geochimica et Cosmochimica Acta, 75(16), 4416–4425. https://doi.org/10.1016/j.gca.2011.05.004

Watkins, J. M., Hunt, J. D., Ryerson, F. J., & DePaolo, D. J. (2014). The influence of temperature, pH, and growth rate on the δ¹⁸O composition of inorganically precipitated calcite. Earth and Planetary Science Letters, 404, 332–343. https://doi.org/10.1016/j.epsl.2014.07.036